<ART>35 years of reforms: A panel analysis of the incidence of, and employee and employer responses to, social security contributions in the UK
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Authors: Stuart Adam, David Phillips, Barra Roantree
DOI: 10.1016/j.jpubeco.2018.05.010
Year: 2019  |  Pages: 29-50
ASJC codes: 2002, 2003
Keywords: Labor demand, Labor supply, Social security contributions, Tax incidence, Taxable income elasticities

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<h>ABSTRACT</h>
--------

We examine the effects of employee and employer social security contributions (SSCs) on labor cost, hours of work, and labor cost per hour, using a long running panel dataset that allows us to exploit 35 years of policy reforms in the United Kingdom. We find that reductions in marginal rates of employee – but not employer – SSCs have positive effects on labor cost that operate through hours of work, while labor cost falls much more when average employer SSCs rates are reduced than when average employee SSCs rates are reduced, with most of this differential effect coming through reductions in hourly labor cost. We interpret this as evidence that employees change their hours in response to SSCs, but that in the short- to medium-run at least, the formal incidence of SSCs can matter for their behavioral impacts and economic incidence.

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<h>INTRODUCTION</h>
------------

Social security contributions (SSCs) make up a large part of the labor tax wedge in
advanced economies, typically raising more revenue than the personal income tax.1 And,
unlike income taxes, they are typically levied on both employers and employees, and only
on labor earnings. Yet the large literature on the elasticity of taxable income (ETI) that
emerged from the seminal papers of Feldstein (1995, 1999) focuses mainly on the response
of overall taxable income to income tax changes, rather than of labor earnings to SSCs,
and it generally takes as given that the economic incidence is on the individual taxpayer.
Meanwhile a parallel literature has developed investigating the incidence of SSCs which
generally ignores the possibility of non-hours responses (e.g. effort) at the heart of the
ETI approach, and sometimes does not account for any behavioral response at all, instead
interpreting changes in earnings following SSCs reforms as evidence of incidence.
Moreover, surprisingly few studies directly address the question of whether the effects of
employer and employee contributions differ. In this paper, we exploit 35 years of reforms
to SSCs in the United Kingdom and a long-running panel dataset on the earnings and hours
of employees to provide evidence on the effects of employer and employee SSCs, considering
both taxpayer responses and incidence. Specifically, these data and policy reforms allow
us to utilise a panel regression approach to contribute to the literature in three
interrelated ways. First, we contribute to the ETI literature by estimating the effects of
SSCs on individuals' labor earnings, which is relatively under-studied. Second, we bring
together the ETI and incidence literatures by examining what can be said about both
incidence and behavioral responses, aided by being able to separate out effects of both
marginal and average SSC rates on both hours of work and hourly wages. And third, we
assess whether the economic incidence of, and behavioral responses to, SSCs are affected
by their formal incidence, exploiting reforms that provide independent variation in
employee and employer SSC rates. Our results suggest that the effects of employee and
employer SSCs differ significantly, at least for the first year or so. Marginal rates
matter for employee but not employer SSCs: we estimate a compensated elasticity of labor
cost (that is, earnings + employer SSCs) with respect to the marginal employee net-of-SSC
rate of around 0.2–0.3 – a response that operates mainly through hours of work – whereas
marginal rates of employer SSCs have no significant effects. In contrast, average rates of
employer SSCs affect labor costs much more than average rates of employee SSCs, and most
of this effect comes via hourly labor costs rather than hours of work. We interpret this
as evidence that employees change their hours in response to SSCs, but that – at least in
the short-to-medium run – the formal incidence of SSCs affects their behavioral impact as
well as their economic incidence. Within the ETI literature, a small number of papers do
examine the responsiveness of specifically labor earnings to income taxation, finding
lower elasticities than are typically estimated for overall taxable income.2 But few
studies have attempted to estimate the elasticity of taxable earnings with respect to the
SSC rate. Two recent working papers, Tazhitdinova (2015) and Adam et al. (2017), find
levels of bunching of employees' earnings at SSC thresholds in the UK that are consistent
with small behavioral elasticities for SSCs too.3 Closer to the present analysis, Lehmann
et al. (2013) estimate the response of labor cost to changes in marginal and average rates
of income tax and employer SSCs in France using panel data. They find an elasticity with
respect to the marginal net-of-income-tax rate of 0.2, but virtually no effect of the
marginal employer SSC rate. They find an elasticity with respect to the average net-of-
income-tax rate of −0.44 (although this is statistically insignificant), and an elasticity
with respect to the average net-of-employer-SSC rate of −0.866. Our results for labor cost
show a broadly similar pattern. Lehmann et al.'s preferred interpretation of their
findings is that wage stickiness prevents employer SSCs from being shifted to employees in
the short term – statutory incidence matters4 – and that employees' labor supply is
reduced by higher marginal rates of income tax. Yet responses to average net-of-tax rates
can pick up income effects as well as incidence. And if wages are determined by a bargain
between employers and employees, changes in marginal rates of tax, holding average rates
fixed, can lead to changes in negotiated wage rates, and hence labor cost, even if there
is no change in labor supply (Lockwood and Manning (1993); Pissarides (1998)). Thus
responses to marginal tax rates may pick up (changes in) the incidence of SSCs as well as
behavioral responses. Our data allow us to shed further light on the relative roles of
behavioral responses and incidence. We decompose labor cost into hours of work and labor
cost per hour, and perform separate regressions for each. Estimates from these hours and
hourly labor costs regressions show that the effects of marginal rates of employee SSCs
operate through hours of work, while most of the effects of average employer SSCs rates on
labor cost come through hourly labor cost. We consider this stronger evidence that
employees respond (on the intensive margin) to employee SSCs, and that the formal
incidence of SSCs matters for their behavioral impacts and incidence in the short-to-
medium-run time frames examined by us and Lehmann et al. Understanding incidence is key
for the interpretation of ETIs. An implicit maintained assumption in most of the ETI
literature that the incidence of taxes is on the individual in question is what allows
estimated coefficients on marginal and average net-of-tax rates to be interpreted as
individual substitution and income effects, respectively. Following Diamond and Mirrlees
(1971), Saez et al. (2012a) point out that shifting of the burden of taxation between
employees and employers does not affect its overall efficiency cost, nor optimal tax
rates. But the efficiency cost implied by employees' earnings responses to taxation does
depend on whether the effect on earnings reflects incidence or underlying behavioral
change. If a change in earnings reflects shifting of the tax burden rather than a change
in the amount of work being done, then the change in the employee's earnings will be
balanced by an opposite change in their employer's income (or the income of whoever the
burden is ultimately shifted to/from), which will usually also be taxed. In that case the
change in employees' taxable earnings does not give the full picture of the change in all
tax bases, or the overall fiscal externality, which is relevant for assessing the economic
efficiency effects of tax policy.5 While the ETI literature has mostly sidestepped
questions of incidence, a separate literature on the incidence of labor taxation has
evolved in parallel which mostly sidesteps the issue of non-hours-of-work labor supply
responses that are at the heart of the ETI literature, and often ignores hours responses
as well.6 As a result, there is a risk that behavioral responses confound estimates of tax
incidence. For example, Gruber (1997) and Anderson and Meyer (1997, 2000) find that firms
seeing bigger reductions in employers' SSCs (as a result of reforms in Chile and the
United States respectively) increased their employees' earnings roughly one-for-one, while
employment in the firms was unaffected. They interpret this as evidence that the incidence
of employer SSCs in these cases is largely, or fully, on workers.7 But it could be the
case that part of the change in observed earnings instead reflects increases in effort or
hours induced by the SSC rate changes. Putting aside this issue, on average studies find
two-thirds of the incidence of labor taxes to be on employees, according to the meta-
analysis in Melguizo and Gonzalez-Paramo (2013),8 but there is a very wide range of
estimates.9 This literature, however, tends to focus on the effects of changes in employer
or combined SSC rates; relatively few studies directly examine whether the incidence of
employer and employee taxes are the same. This probably reflects the fact that many
countries' reforms to SSCs affect employee and employer contributions simultaneously and
highly co-linearly, making identification of separate effects difficult. By utilising a
long time period in which there were separate reforms to employee and employer SSCs, we
can examine whether responses to them differ – one of the first studies to investigate
this using micro-data. The few existing studies that address this question are mainly
based on cross-country regressions (such as OECD (1990) and Arpaia and Carone (2004));
they find – as we do – evidence that the incidence differs in the short-term, perhaps
reflecting short-term stickiness of nominal wages. Whether the incidence converges in the
longer run – as standard theory predicts – is less clear, in part because of weak
statistical power in the long-run analyses that examine this issue (CPB et al., 2015). As
with most of the incidence literature, we use ‘incident on employers’ as a shorthand to
mean ‘incident on someone other than the employee whose tax rate changed’. Of course, the
ultimate burden of a tax must always fall on real people, not the businesses or
organisations employing them; it may be passed on to the employers' owners, customers
and/or suppliers, and thence perhaps more widely via general equilibrium responses. One
important possibility is that a tax that is not incident on the employee whose tax rate
changes may nevertheless be incident on a broader group of workers: the nature of market
responses may be such that a tax change affecting one small group of employees results not
in a large change in wages for those employees but in a small change in wages for all
employees in the firm, or in an infinitesimal change in equilibrium wages in the wider
market. All we attempt to discern in this paper is how an individual's wage is affected by
the tax rate applied to that individual's earnings; insofar as their net wage is not
reduced one-for-one then we refer to the tax as being at least partly incident ‘on the
employer’, even though the burden may be felt by a wider group of employees rather than by
(say) the employer's shareholders. The paper proceeds as follows. Section 2 describes the
UK's SSC regime, the reforms we use to identify its effects, and the data. Section 3
discusses the identification of behavioral responses and incidence, while Section 4 sets
out our econometric approach. Descriptive statistics and estimation results are presented
and discussed in Section 5. Section 6 concludes.

<hs>  Overview of the UK's system of SSCs</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Like SSC systems in most countries, the UK's system of National Insurance contributions
(NICs) consists of both employer and employee contributions, which are functions of the
employee's gross earnings.10 The NICs rate schedule changed markedly during the period we
analyse (1982 to 2015), and it is those changes that we exploit in this paper. Throughout
this period, earnings below a threshold were exempt from NICs. Before 1985, once earnings
exceeded this threshold (then called the Lower Earnings Limit, LEL), employer and employee
NICs were levied at constant percentage rates on all earnings (including earnings below
the threshold) up to a ceiling called the Upper Earnings Limit (UEL). This created a jump,
or notch, in contributions at the LEL: both marginal and average rates of NICs increased
from zero to the rate payable above the LEL, which at the start of 1985 stood at 9% for
employees and 10.45% for employers. A reform in October 1985 replaced this single large
notch with a series of smaller notches: the jump in marginal and average rates at the
exemption threshold was reduced to 5% each for employees and employers, and a number of
graduated steps were introduced, where higher (marginal and average) rates applied to the
entirety of earnings once earnings exceeded higher thresholds. At the same time, the cap
on employer contributions was abolished so that the highest rate of employer NICs applied
to earnings above the UEL. The effect of this reform on the combined headline employee and
employer NICs schedule can be seen in the black and solid grey lines in Fig. 1. In October
1989, the system of graduated employee contributions was replaced by a single small notch
at the lowest threshold (equivalent to 2% of the threshold) and a single 9% marginal rate
of employee NICs that applied to earnings between the threshold and the UEL. However, the
graduated system of employer NICs with four notches remained in place at that stage until
April 1999, when the remaining notch in the employee NICs schedule, and all the notches in
the employer schedule, were removed. There was also a series of other – generally smaller
– changes in other years.11 The combination of changes in both thresholds and rates, the
move from a notch-based system to a kink-based system via a series of smaller notches, and
the extension of NICs (particularly employer NICs) above the UEL, provides a rich source
of variation across the earnings distribution. Sometimes employer and employee NICs rates
changed together, but other times they changed differentially. Some reforms affected
individuals' marginal and average NICs in similar ways, but other reforms affected them
very differently. This variation allows us to separately identify responses to changes in
both marginal and average rates of both employee and employer NICs. Two additional
features of the NICs system are relevant for our analysis. The first is that, unlike in
many social security systems, the link between NICs paid and benefit entitlements was
limited during our period of analysis. This means that NICs can be thought of largely as a
straightforward earnings tax rather than ‘true’ social insurance. However, there was one
strongly contributory element of the National Insurance system: the earnings-related
component of the state pension. Individuals contributing to a private pension could choose
to forgo this future entitlement and in return pay lower rates of employee and employer
NICs on their earnings: a process known as ‘contracting out’.12 Prior to 1997 our data do
not record whether people were contracted in or out of the earnings-related state pension,
but for the purposes of our analysis we assume that everyone was contracted out
throughout. This is partly because, over the period as a whole – and especially in the
years that provide most of our identifying variation – the majority of employees were
contracted out. But more importantly, even for those employees who were contracted in, the
contracted-out rates are arguably a better measure of the ‘tax wedge’ associated with
NICs: the additional NICs associated with ‘contracting in’ generated additional future
pension entitlements on a roughly actuarially fair basis, so resemble retirement saving
more than a tax insofar as people value these future entitlements. In any case, the
reforms that generate our variation in NICs rates apply to both contracted-in and
contracted-out rates. And crucially, none of the changes in contribution rates over our
period were associated with a corresponding change in benefit entitlements. When an
individual in our data sees their NICs rate change, it simply changes their current budget
constraint, just like a tax; they do not see changes to the implicit savings or insurance
which they might value. The only reason we might expect people to respond to the NICs
changes we use differently from any other tax on earnings is if they (incorrectly)
perceive it differently. The second feature is a reduced rate of employee NICs payable by
married women: 2% at the start of our period, rising to 5.85% by the end. This was (and
remains) available, in exchange for reduced benefit entitlements, to married women who
have been claiming it almost continuously since May 1977. In 1979–80, 4.2 million women
were eligible for this rate, falling to 560,000 in 1995–96 (of whom 340,000 were making
use of it) and fewer than 80,000 by 2000–01. Since our data do not allow us to identify
women eligible for this rate, we assume all women face the standard (contracted-out) rate
of NICs. For this reason, comparisons of our estimates between men and women should be
treated with caution. However, our main findings hold when we restrict our sample to men
only – who are not affected by this issue.

<hs>  Income tax, means-testing and the National Minimum Wage</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In addition to NICs, employees' earnings are also subject to income tax, which until 1990
was usually assessed on joint income for married couples. Our data do not capture whether
an employee is married, or the income of an individual's spouse, meaning we cannot account
for income tax in our analysis.13 Similarly, means-tested benefits and tax credits may
also contribute to the effective tax wedge on an individual's earnings, but such
entitlements always depend on (married or unmarried) couples' joint income and other
characteristics (such as housing costs and the presence and number of children) that are
not observed in our data. If changes to these other elements of the tax wedge were
correlated with changes to the NICs schedule, they might confound estimates of the effect
of SSCs on labor cost or hours. Likewise, the introduction of a National Minimum Wage
(NMW) in October 1999 and subsequent increases in it may confound estimates of the effects
of NICs rate changes if the two are correlated. The NMW was initially set at around 45% of
median hourly pay and directly affected 3.4% of employees, rising to 52% and 5.2%,
respectively, by April 2015 (Low Pay Commission, 2016). The NMW may also affect the
incidence of NICs for low-paid workers by putting a floor below which employers are
legally not allowed to reduce hourly wages. In light of these factors, we test the
sensitivity of our estimates to the exclusion of years following the introduction of the
NMW: 2000 and later. This period saw a significant expansion of in-work means-tested
benefits as well, so excluding these years will also limit any impact of such benefits in
our estimates.

<hs>  The New Earnings Survey Panel Dataset</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The data used in this paper are taken from the New Earnings Survey Panel Dataset (NESPD),
a mandatory survey of employers' payroll records, which collects data on employees'
earnings and hours worked. The target sample frame of the NESPD is civilian employees in
Great Britain whose National Insurance (NI) number ends with a specific pair of digits.
Since the last digits of NI numbers are allocated randomly to all adults and the NESPD
sample uses the same pair of digits each year, in principle this should deliver a random
1% panel sample of employees, from the late 1970s onwards. In practice, despite the survey
supposedly being mandatory, non-response reduces the sample to around 0.7% of employees on
average over the period. Nevertheless, at around 165,000 individuals per year the NESPD
contains a much larger sample than is available in other UK datasets of hours and earnings
(such as the Labor Force Survey and the Living Costs and Food survey), and it does not
suffer from the same degree of measurement error as responses are provided by employers
with reference to their payroll and employment records.14 We do not observe people when
they are not employed, and cannot distinguish whether someone who is absent from a
particular year of data was not working, was self-employed, or was working for an employer
who failed to respond to the survey. As a result, the analysis in this paper focuses on
those employed in consecutive waves of the NESPD, and estimates therefore do not account
for any extensive margin responses to NICs. The NESPD records weekly hours and gross
earnings – including overtime, commission, performance-related pay, etc., but excluding
benefits in kind and employer pension contributions – for the pay period that includes a
particular date in April each year (termed the survey reference date). This corresponds
closely to the tax base for NICs, which is levied on a very similar definition of
earnings, separately by pay period.15 However, the collection of these data in April is
not ideal in the context of our study. This is because the UK's fiscal year runs from
April 6th of one year to April 5th of the next, and changes to NICs often take effect at
the start of the fiscal year. Furthermore, the NICs due on the earnings in the pay period
captured by the NESPD depends upon the NICs system in place on the date those earnings
were actually paid. Thus if payment for the pay period in question was made on or after
April 6th the NICs system of the ‘new’ fiscal year would have applied. This will be the
case for a large majority of our sample, including those paid on a calendar month basis at
the end or middle of the month and those paid on a weekly basis unless the reference date
is very near the start of April. For such employees, the earnings and hours captured by
the NESPD will thus relate to the pay period immediately following any change to NICs
taking effect at the start of the fiscal year. However, for those paid on April 5th or
earlier, the NICs system of the ‘old’ fiscal year would apply. This includes those paid on
a calendar month basis at the start of the month, and for the two years when the survey
reference date was at the start of April, could include some of those paid on a weekly
basis. For such employees, the earnings and hours captured by the NESPD will actually
relate to the pay period immediately before any change to NICs taking effect at the start
of the fiscal year. Unfortunately, the NESPD does not record either the date an employee
is paid or the length of their pay period. In what follows we proceed by assuming the
earnings we observe are subject to the NICs schedule of the fiscal year just beginning, as
will be the case for the vast majority of our sample. This means we are typically
estimating very short-run responses to changes in NICs rates; the effect of reforms
implemented earlier in the same month. However, two of the biggest reforms to the NICs
schedule (in 1985 and 1989) were implemented in October, not April, so a significant part
of our identifying variation comes from reforms implemented around six months before the
earnings and hours we observe. In addition, changes to the NICs schedule are invariably
announced at least a few months in advance (so that payroll software can be ready in time
to operate it, among other reasons), so our estimates will capture the effects of reforms
announced some time beforehand. In those rare cases where the earnings we observe are in
fact subject to the NICs schedule of the tax year just ending, our estimates will capture
only earnings responses in anticipation of a reform's implementation, and the reform's
implementation will instead be reflected in the subsequent year's earnings.

<hs>  Effects on labor cost</hs>
  ~~~~~~~~~~~~~~~~~~~~~

We now turn to our discussion of the identification of behavioral effects and incidence.
We define labor cost (Z) as the sum of gross earnings (W) and employer NICs, and net-of-
NICs earnings (C) as gross earnings minus employee NICs. Gross earnings are taken directly
from the NESPD data, and both employee and employer NICs calculated using the NICs
schedule. Such an interpretation relies on labor demand being perfectly elastic, and
therefore the incidence of a tax – in this case NICs – being purely on the employee. If
one allows for less than perfectly elastic labor demand – and therefore the prospect of at
least partial incidence of NICs on employers – the β coefficients will pick up a
combination of labor supply responses, labor demand responses, and shifting of incidence.
With information on labor cost alone, it is difficult to disentangle these effects.
Consider first the coefficients on average net-of-NICs rates (βZ,ρR and βZ,ρE). As well as
capturing income effects, they will also reflect the incidence of NICs. For example, if
labor cost increases in response to a rise in the average rate of employee NICs, that
could reflect employees' working harder to make up the loss of income (an income effect),
some shifting of the additional tax burden onto employers (incidence), or some combination
of the two effects. In order to identify either income effects or incidence, one needs to
assume the other: for example, assuming zero income effects allows one to interpret the
coefficients in terms of incidence, while assuming full incidence on employees allows one
to interpret the coefficients in terms of income effects. Changes in the extent to which
NICs are shifted also mean that positive coefficients on marginal net-of-NICs rates (βZ,τR
and βZ,τE) cannot be interpreted purely as compensated labor supply and demand responses
either. In wage bargaining models, reductions in marginal tax rates, holding average rates
fixed, can lead to higher wages, and hence higher labor costs, even absent changes in
effort or hours of work (Lockwood and Manning, 1993; Pissarides, 1998).20 This is because
lower marginal rates increase the marginal benefit to employees of bargaining for higher
wages and reduce the cost to employers of acceding to these demands. Again, interpretation
of these effects as behavioral responses requires making an assumption about the effects
of marginal rates on incidence (and vice versa).

<hs>  Effects on hours of work and hourly labor cost</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The availability of hours of work in our data allows us to decompose changes in labor cost
into changes in hours of work (H) and changes in labor cost per hour (Z/H). This can shed
further light on the roles of incidence and behavioral responses in explaining changes in
overall labor cost. Meanwhile, if leisure is a normal good, income effects would mean an
employee would want to reduce their hours of work when their average net-of-NICs rate
increases (holding the marginal net-of-NICs rate fixed). Potential responses to average
rates by employers are more complicated. A higher average net-of-NICs rate, holding the
marginal net-of-NICs rate constant, can be viewed as providing a lump sum transfer per
employee. As well as inducing employers to hire more people and produce more output (both
responses which our analysis cannot pick up), this might also prompt employers to change
the hours of existing employees, for example by producing a given level of output with
more workers but fewer hours per worker. Changes in labor cost per hour could also reflect
behavioral response. For instance, when their net-of-NICs rate changes, employees may
adjust their effort per hour worked, potentially resulting in a change in gross earnings
(and hence labor cost) per hour. As with hours of work, there would be positive
substitution effects for changes in marginal net-of-NICs rates and negative income effects
for changes in average net-of-NICs rates. Employers may also adjust the way in which they
compensate employees, such as making more or less use of benefits-in-kind or pension
contributions: thus changes in the monetary labor cost per hour that we measure may not
correspond to changes in overall labor cost per hour. However, we cannot empirically
distinguish between such effects and changes in labor cost per hour that reflect the
economic incidence of NICs. For instance, if NICs are partly incident on employers, an
increase in the average net-of-NICs rate would lead to a reduction in labor cost per hour.
This is observationally equivalent to an income effect on employees' effort of the kind
mentioned above. Thus we cannot draw clear conclusions about the incidence of NICs from
reduced-form estimates of their effect on hourly labor cost unless we rule out – or make
precise assumptions about the size of – non-hours behavioral responses of the kind that
originally motivated the ETI literature: changes in effort per hour worked and shifts in
compensation to forms not liable for NICs. But if, for instance, one is willing to rule
out such responses, changes in hourly labor costs will reflect changes in underlying wage
rates, therefore capturing incidence effects that remain ambiguous when studying labor
cost alone. In particular, the coefficients on average net-of-NICs rates in an hourly
labor cost equation (βZ/H,ρR and βZ/H,ρE) would capture the average incidence of NICs.
Coefficients of 0 (labor cost unaffected by the net-of-NICs rate) would indicate that NICs
were fully incident on employees, while coefficients of −1 (labor cost moving one-for-one
with changes in NICs) would indicate incidence fully on employers. However, as already
highlighted, in a labor market characterised by wage bargaining compensated changes in
marginal net-of-NICs rates can have effects on underlying hourly wage rates and hence
hourly labor costs. In particular, an increase in the marginal net-of-NICs rates would
increase the marginal benefit to employees of bargaining for higher wages and reduce the
cost to employers of acceding to those demands, raising the hourly labor cost that
results. Such an effect on hourly labor cost would be observationally indistinguishable
from a substitution effect operating via the effort or compensation-form margin. One can
therefore draw inferences about the effect of marginal net-of-NICs rates on incidence (and
from this infer something about the wage determination process) only if one is willing to
rule out non-hours behavioral responses, and vice versa.

<hs>  Differential effects of employee and employer NICs</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

If we can reject (any of) these conditions then we can conclude that this ‘invariance of
incidence proposition’ does not hold within the timeframe we measure changes in hours and
labor costs. If we believed we were picking up the long-run impact of NICs then we would
have to move beyond these simple benchmark models of the labor market towards, for
instance, a model where collective wage bargains are struck over groups of heterogeneous
workers, or where bargaining is based on gross wages (as opposed to labor costs and net
wages).21 It is not clear that sticky wages implies that βZ,τR = 0: employers could
respond to compensated changes in the marginal NICs they pay on their employees' wages by
changing the hours they offer individual employees. These hours changes would affect labor
cost per employee. This test would be valid only if hours of work were also sticky. In
that case, though, we would not expect hours to respond to changes in employee NICs rates
either.

<hs>  Basic specification</hs>
  ~~~~~~~~~~~~~~~~~~~

Xi,t is a vector of controls, including year dummies (to pick up, for instance, the effect
of inflation), a cubic of the employee's age, their sex, and whether they are in the same
job in year t as year t − 1, as well as controls for differential trends in labor costs in
different parts of the labor costs or hours distributions (discussed below). εi,t,z is an
error term that captures unobserved and time-varying heterogeneity. It is well known from
the labor supply and ETI literatures that various econometric challenges arise with
estimation of such equations (Saez et al., 2012a). The first is a potential simultaneity
bias. Because of the nonlinearity of the employee and employer NICs schedules, the
marginal and average net-of-NICs rates τi,tE and τi,tR are themselves functions of the
left-hand-side variable. Instruments are therefore required to identify the effect of
NICs. The long-established standard approach to this problem, proposed by Auten and Caroll
(1999), uses changes in the log net-of-tax rates holding earnings at their year t − 1
level as an instrument for actual changes in the net-of-tax rates. This does not address
two further econometric issues: that mean-reversion in income processes and differential
secular trends in income can confound estimates of the β coefficients, especially when tax
rate changes affect different parts of the income distribution differently. Again
following Auten and Caroll (1999), the literature has traditionally tried to deal with
these issues by including functions of income/earnings in year t − 1 and/or year t − 2 in
the regressions. However, Weber (2014) shows that instruments based on t − 1
income/earnings cannot be exogenous if there is mean reversion even if such controls are
used. Instead, she proposes instrumenting changes in the net-of-tax rates using changes in
these tax rates calculated holding earnings fixed at its level in an earlier year t − k
(rather than t − 1) where k ≥ 2.22 The lag k should be chosen so that it is far enough
before the year in question that earnings in year t − k are unaffected by any transitory
shocks affecting earnings in years t − 1 and t, but not so far that the instrument is a
weak predictor of the actual change in tax rate observed. It is possible to test whether a
particular instrument is exogenous, conditional upon the assumption that other excluded
instruments (for example, based on longer lags) are exogenous using a Difference-in-Sargan
test. As we show in Table E3 of Appendix E, we, like Weber, reject the exogeneity of
instruments based on earnings in year t − 1 (the p-values of the tests are 0.000 for each
of labor cost, hours and hourly labor cost). But Table E2 shows we cannot reject the
exogeneity of instruments based on earnings in year t − 2 (p-values of 0.16, 0.74 and
0.24, respectively).23 We therefore use instruments based on earnings in year t − 2 in our
main specification.24 While our use of Weber-type instruments should deal with the problem
of mean reversion, it will not deal with the problem of longer-term differential earnings
trends. For instance, during the 1980s, earnings inequality was increasing significantly
in the UK (Blundell and Etheridge, 2010). At the same time, changes in NICs (most notably
in 1985) reduced average NICs rates at the bottom of the earnings distribution, and
increased them at the top. The risk is that one would inappropriately attribute secular
changes in relative labor costs to the tax reform, biasing estimated coefficients. To
control for differential trends in earnings and hours at different parts of the
distribution, we include controls based on lnZi,t−2. Following Eq. (3.2)., the changes in
average net-of-NICs rates included in our regressions (∆ ln ρi,tR∣ and ∆ ln ρi,tE∣) are
calculated holding earnings fixed at year t − 1. Lehmann et al. (2013) show that using the
actual change in average net-of-tax rates or virtual income between years t − 1 and t
would lead to inconsistent estimates, even if instrumented. As with the changes in
marginal net-of-NICs rates, we instrument these using changes in average net-of-NICs rates
calculated holding earnings fixed at year t − 2 (and in robustness checks, t − 3) levels.

<hs>  Including lagged changes in NICs</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Examining changes in labor cost, hours and labor cost per hour between years t − 1 and t,
and relating this to changes in tax rates between year t − 1 and t may pick up only very
short run behavioral effects and incidence shifting, especially given the timing of our
data collection (discussed in Section 2.3). The traditional approach to capturing longer-
run responses is to use panel lengths of longer than one year: for instance, calculating ∆
ln Zi,t =  ln Zi,t −  ln Zi,t−2 or ∆ ln Zi,t =  ln Zi,t −  ln Zi,t−3 rather than
calculating ∆ ln Zi,t =  ln Zi,t −  ln Zi,t−1. This is the approach taken by Gruber and
Saez (2002), among others. However, such an approach will not accurately measure the long-
run effect, but rather (at best) an average of responses over the extended period. And if
there are multiple reforms, estimation may be confounded, with estimated elasticities not
representing even an average of shorter- and longer-run responses.25 βZ,τR,0, for
instance, picks up the immediate effect of reforms: that is, the effect of changes in the
marginal net-of-employer-NICs rate between years t − 1 and t on the change in labor cost,
Z, between years t − 1 and t. βZ,τR,1 picks up the (additional) effect in the subsequent
year: that is, the effect of changes in the marginal net-of-employer-NICs rate between
years t − 2 and t − 1 on the change in labor cost, Z, between years t − 1 and t. The
overall effects of a change in NICs taking effect between t − 2 and t − 1 on labor cost in
year t can be calculated by adding the coefficients on the contemporaneous and lagged
changes in tax rates (e.g. βZ,τR,0 + βZ,τR,1). In Table E1 of Appendix E we also show
estimates for regressions that include only lagged changes in NICs rates. As with
contemporaneous changes in tax rates, it is important to instrument Δlnτi,t−1 and
Δlnρi,t−1∣ appropriately. We do this using instruments based on earnings held fixed at
year t − 3 levels as in our basic specification examining short-run responses. We again
test the robustness of results to using instruments based on earnings held fixed at year t
− 4 levels.

<h>DESCRIPTIVE STATISTICS AND RESULTS</h>
----------------------------------

Our estimation sample consists of approximately 1.7 million observations.27 Men make up
just under 6-in-10, those aged 50 or over make up 3-in-10 and those working in the public
sector in both years t − 1 and t make up 1-in-3 of the estimation sample.28 This sample is
somewhat more male, older and more likely to be in the public sector than the full NESPD
sample. This reflects the fact that individuals with these characteristics are more likely
to be observed for the requisite number of years. Men, for instance, are less likely to
move in and out of work, and to have the very low levels of earnings that mean they may
not be sampled even if working.

<hs>  Identifying variation in NICs rates</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As discussed in Section 2.1, there were particularly significant reforms to NICs in
October 1985, October 1989 and April 1999. Fig. 2a to f show the (log) changes in the
average and marginal employee and employer net-of-NICs rates between 1985 and 1986 (Fig.
2a and b), between 1989 and 1990 (Fig. 2c and d) and between 1998 and 1999 (Fig. 2e and
f). Overlaid on these NICs-change schedules are histograms showing the density of the
earnings distribution. Fig. 2a, for instance, shows that that changes in employee NICs
rates in 1985 were largest towards the bottom of the earnings distribution, although
sufficiently far up for there to be significant sample sizes. It also shows that marginal
and average employee NICs rates changed in almost exactly the same way, with the exception
of an increase in marginal NICs rates for a narrow range of earnings around £265 per week,
associated with the UEL increasing slightly faster than average earnings growth. Fig. 2b
shows a similar picture for employer NICs for the bottom part of the earnings distribution
– although changes in these extended further up the earnings distribution. The extension
of full employer NICs above the UEL led to a large discrete fall in the marginal net-of-
NICs rate, and to rises in the average net-of-NICs rate that smoothly increased above this
point. The 1985 changes were substantial: increasing mean net-of-NICs rates by up to about
5% in some cases and reducing them by up to about 10% in others. Fig. 2c and d likewise
show the effect of the 1989 reform, which provides significant differential variation in
average and marginal rates of employee NICs, while Fig. 2e and f illustrate the variation
in average and marginal rates of employer NICs from the 1999 reform. Each of these reforms
can thus make a significant contribution to disentangling the effects of different
elements of the NICs regime. The figures also show clearly that the 1985, 1989 and 1999
reforms to NICs generated non-convex changes in the budget sets facing employees and
employers. In such circumstances, changes in NICs at levels of earnings higher than
existing earnings (and so which affect neither marginal nor average NICs rates at existing
earnings) can lead to discrete jumps in earnings in response. Such effects are not
accounted for in the log-linear specifications we estimate in this paper. Our estimates
therefore come with the caveat that they may not pick up all intensive margin responses
(recall that our data do not allow us to pick up extensive margin responses at all). Since
the 1985 reforms affected employee and employer average and marginal NICs rates very
similarly (except towards the very top of the earnings distribution), and since the 1989
and 1998 reforms each significantly affected only one of employee or employer NICs, it is
not possible to use a single reform to identify the separate effects of changes in both
average and marginal rates of both employee and employer NICs. In addition, as shown in
Appendix C, mean reversion in earnings is a significant issue when estimating the impact
of reforms that predominantly affect those with low earnings, making reliance on a single
reform problematic. The use of instruments based on earnings in year t − 2 (or t − 3), and
the inclusion of functions of year t − 2 earnings as control variables, is designed to
minimise the impact of such mean reversion. However, as discussed in Kleven and Schultz
(2014), having reforms that both increase and decrease rates of a tax on a given part of
the income/earnings distribution is also beneficial (as the effects of mean reversion work
in opposite directions for tax increases and decreases). We therefore turn to examining
variation in tax rates using the full panel, covering reforms between 1982 and 2015. Table
1 shows the mean and standard deviation of (100 multiplied by) the changes in log net-of-
NICs rates, by position in the earnings distribution. It shows that marginal net-of-
employee-NICs rates fell over the period as a whole, especially in the lower-middle and
middle part of the earnings distribution. This reflects increases in the statutory rates
of NICs. Larger reductions in the marginal net-of-employer-NICs rates at the top of the
earnings distribution reflect, in large part, the uncapping of employer NICs in October
1985. The abolition of the notches at the LEL means that average net-of-NICs rates
increased towards the bottom of the earnings distribution for employees, and a long way up
the earnings distribution for employers (though the uncapping of employer NICs means
average net-of-employer-NICs rates still fell at the very top of the distribution).
Changes in marginal and average NICs rates over the last 30 or so years therefore differ
significantly, in principle allowing identification of the effects of both. But our
identification does not come solely from variation across the earnings distribution. The
standard deviations of changes in log net-of-NICs rates for given parts of the earnings
distributions are much larger than the mean changes, reflecting a pattern of increases and
decreases in NICs rates at specific parts of the distribution in different years. Fig. 3
shows significant variation in changes in log net-of-NICs rates both across and within
years.29 Panels (a) and (b) show that the largest changes to mean NICs rates were in years
when the main NICs rate changed: for instance, 1994 for employees only and 2003 and 2011
for both employees and employers. However it is the variation in NICs rate changes within
years that matters most for identification (given that we include year dummies in our
regressions). Panels (c) and (d) show that in many years there was relatively little
variation but the major reforms of October 1985, October 1989 and April 1999 are
associated with clear ‘spikes’ in the standard deviation of NICs rate changes (in 1986,
1990 and 1999). There was also significant variation in 1997, 2000 and 2011, associated
with further policy changes.30

<hs>  Estimation results</hs>
  ~~~~~~~~~~~~~~~~~~

Before separately estimating the effects of employee and employer' NICs, we first estimate
the responsiveness of labor cost to the overall rate of NICs. The results of these
regressions are shown in Table 2. Column 1 shows estimates where our set of controls Xi,t
includes a cubic of lnZi,t−2; column 2 shows estimates based on a quintic of lnZi,t−2,
and; column 3 shows estimates based on a 10-piece spline of lnZi,t−2. Estimated
coefficients are broadly stable across specifications and later results are shown only for
quintic controls. βZ,τNI,0 measures the effect of changes in the overall marginal net-of-
NICs rate on labor cost: estimates are positive, albeit small and not quite statistically
significant. This would imply that labor cost is relatively unresponsive to compensated
changes in marginal NICs rates, suggesting a relatively small deadweight loss of the tax.
On the other hand, estimates of βZ,ρNI,0 (which measures the effect of changes in the
average net-of-NICs rate on labor cost) are negative, large and highly statistically
significantly different from 0, but not from −1. These estimates can be interpreted in
several ways. If we assume that the incidence of NICs is fully on employees, then this
would imply very large income effects. Alternatively, if we assume that income effects are
small, then the estimates would imply that the incidence of NICs changes was largely on
employers. Finally, the results are consistent with moderate-to-large income effects and
sharing of the burden of NICs between employees and employers. As noted above, though, the
effects of employee and employer NICs may differ, especially in the short-to-medium term
(e.g. due to wage stickiness). Column (1) of Table 3 shows coefficients estimated
separately for employee and employer NICs. Our estimate of βZ,τE,0 is statistically
significant and positive (0.25), while βZ,τR,0 is near zero. These results are very
similar to those of Lehmann et al. (2013) for France, where they found positive
compensated elasticities for marginal net-of-income tax rates and zero elasticities for
employers' SSCs. βZ,ρE,0 is negative, of a moderate size, but not statistically
significantly different from 0 (it is statistically significantly different from −1,
however). βZ,ρR,0 is also negative, but much larger: indeed, statistically significantly
less than −1. We can reject both that βZ,τE,0 = βZ,τR,0 and that βZ,ρE,0 = βZ,ρR,0: the
statutory incidence of NICs matters for its (immediate) impact on labor costs. Recall that
in the absence of income effects, βZ,ρR,0 = −1 would indicate 100% incidence of employer
contributions on the employer. One possible explanation for a coefficient statistically
significantly less than −1 is that changes in average employer NICs rates are ‘over-
shifted’ to employers, as can happen in some models. It might also be natural to view
βZ,ρR,0 < −1 as a combination of statutory incidence with standard income effects.
However, if employers are bearing the burden of employer contributions, there is no change
in earnings which can generate an income effect for the employee in question. This is an
issue to which we return below. In columns (2) and (3) we decompose the changes in labor
cost into changes in hours of work and changes in hourly labor cost, to shed further light
on the role behavioral response and incidence play in our findings. For hours of work, we
find a positive compensated elasticity for employee NICs (βH,τE,0) but a zero compensated
elasticity with respect to employer NICs (βH,τR,0). In contrast, for hourly labor cost,
elasticities with respect to employee NICs (βZ/H,τE,0) and employer NICs (βZ/H,τE,0) are
virtually identical. This provides strong evidence that the differences in responses of
overall labor cost reflect differential behavior responses to changes in marginal employee
and marginal employer NICs, rather than differential effects of NICs progressivity on
hourly wage rates (and thus hourly labor costs). Our results contrast with those of
Blomquist and Selin (2010), who find that increases in earnings in response to a reduction
in marginal income tax rates are largely driven by increases in hourly earnings rather
than hours of work, at least for men.31 Our results also differ somewhat from Lehmann et
al. (2013), who find that labor cost responses are driven almost entirely by those working
less than a full year – suggestive that weeks worked per year respond more than hours per
week. However, given that NICs are levied per pay period (rather than on an annual basis),
in our context it makes sense that any hours response to marginal NICs rates takes place
at the ‘intensive’ rather than the ‘extensive’ margin: changes in the number of pay
periods worked will not affect the amount of NICs paid in any given pay period. It is also
worth noting that because of the timing of our data, these estimates may reflect short-
term inter-temporal responses to changes in NICs: shifting hours of work from a pay period
with a higher marginal employee rate to one with a lower marginal employee rate. This is
an issue we return to when discussing estimates that include lagged changes in net-of-NICs
rates. Turning to responses to average net-of-NICs rates, we find hours-of-work
elasticities for employee (βH,ρE,0) and employer (βH,ρR,0) NICs that are similar to each
other and both statistically significantly below 0. For hourly labor costs, the elasticity
for the average net-of-employee-NICs rate is not statistically significantly different
from 0, while that for the average net-of-employer-NICs rate is not statistically
significantly different from −1. How should we interpret these results? βZ/H,ρE,0 = 0 and
βZ/H,ρR,0 =  − 1 is consistent with the economic incidence of NICs following statutory
incidence: employees bear changes in the amount of employee NICs due, and their employer
bears changes in the amount of employer NICs due. In this context, a negative elasticity
of hours with respect to the average net-of-employee-NICs rate might naturally be
interpreted as indicative of income effects: higher post-NICs pay inducing individuals to
‘buy’ more leisure by reducing their hours of work. However, income effects cannot
rationalise the negative elasticity of hours with respect to the average net-of-employer-
NICs rate: if employers are bearing the burden of employer contributions then there is no
change in earnings which can generate an income effect for the employee in question. Why
then should a reduction in the average employer NICs rate (controlling for the marginal
rate) cause employers to reduce their employees' hours of work? One reason, highlighted in
Section 3.2, is that it can be thought of as providing firms with an extra lump sum per
worker. Given this, one response for firms is to adjust their production technology to use
more workers, each working fewer hours. As we cannot capture extensive margin responses,
our regressions will simply pick up the reduced hours per worker. However, while this
mechanism is possible, it seems unlikely to be sufficiently large to explain the size of
the estimated coefficients. There remains the possibility that the result is driven by
some omitted factor (perhaps a non-NICs reform or a macroeconomic shock) with a large
effect on hours of work that is correlated with the variation in NICs rates that
identifies the effect of average employer NICs changes. For now, this result remains a
puzzle within our broader findings.

     <hss>Adding lagged NICs changes</hss>

        Panel (B) of Table 3 adds lagged changes in net-of-NICs rates as regressors. This
        allows us to examine whether the effects of changes in NICs differ after an
        additional year, with overall effects obtained by adding the coefficients for the
        contemporaneous and lagged changes together (e.g. βX,τE,0 + βX,τE,1)32. Two
        findings stand out. First, effects for contemporaneous changes are broadly similar
        to those in Panel (A): adding lagged changes in NICs rates does not affect the
        general pattern of results for contemporaneous changes – statutory incidence
        continues to matter for responses to both marginal and average net-of-NICs rates.
        Second, while the coefficients on the lagged changes in marginal and average net-
        of-NICs rates are sometimes statistically significant, so that effects of NICs
        changes differ after a year, there is no evidence of a move towards employee and
        employer NICs having a more similar effect after a year. For instance, the gap
        between the effect of average employee (βz/h,ρE,0 + βz/h,ρE,1) and average
        employer (βz/h,ρR,0 + βz/h,ρR,1) net-of-NICs rates on hourly labor costs grows, if
        anything, after a year, rather than shrinking (statistically speaking, we cannot
        reject the hypothesis that the gap remains unchanged). In other words, if employer
        NICs begin to be shifted to employees (or vice versa), this does not appear to
        occur within the year or so following a NICs change. Similarly, the gap between
        the effects of marginal employee (βh,τE,0 + βh,τE,1) and marginal employer
        (βh,τE,0 + βh,τE,1) NICs rates on hours of work also grows. The statistically
        significant positive coefficient on the lagged change in the marginal net-of-
        employee-NICs rate suggests that the full behavioral response to marginal employee
        NICs rates does not occur immediately. Thus (temporary) inter-temporal responses
        to changes in marginal employee NICs rates are unlikely to be driving our results
        for specifications including contemporaneous changes in net-of-NICs rates only.

     <hss>Robustness checks</hss>

        In Appendix E we investigate the robustness of the baseline estimates reported in
        Panel (B) of Table 3 to different instruments and labor cost controls, and to
        restrictions on the years of data included in the estimation sample. Estimates are
        robust to using instruments based on year t − 3 earnings, but not instruments
        based on year t − 1 earnings. However, the Difference-in-Sargan statistics for the
        latter instruments are all highly statistically significant, suggesting that they
        are unlikely to be exogenous (probably due to mean reversion). Estimates are also
        generally robust to excluding years where the survey reference date was before or
        close to the start of the fiscal year, and when we restrict ourselves to years
        with major reforms. We also find the same qualitative differences between the
        responses of labor costs and hours of work to employee and employer NICs when we
        restrict our sample to the period up to 1999, the point at which the National
        Minimum Wage was introduced. In particular, the effects of changes in average net-
        of-employer-NICs rates on labor cost per hour are very similar to those obtained
        for the full sample, suggesting that the introduction of the NMW did little to
        affect the overall incidence of employer NICs (at least across the earnings
        distribution as a whole). But there are some non-trivial differences in the point
        estimates of the coefficients on changes in marginal net-of-employee-NICs rates in
        the hours-of-work regressions for this sub-period. These differences suggest that
        we should be cautious about drawing overly strong conclusions about the precise
        scale and dynamics of hours-of-work responses to employee SSCs.

     <hss>Demographic sub-groups</hss>

        Estimates for selected demographic groups can be found in Appendix F. Again, the
        clearest findings from analysis of the full sample hold: hours responses to
        changes in marginal employee NICs rates are larger than marginal employer NICs
        rates; and hourly labor cost responses to average employee and employer NICs rates
        suggest that statutory incidence matters for at least a year or so following a
        reform. Furthermore, as one might expect, responses differ for workers in the
        public versus private sector. There is evidence, for instance, of responses to
        changes in marginal employee NICs rates occurring more quickly in the private
        sector than the public sector. There is also evidence, after one year, of some
        shifting of the burden of employee NICs to employers in the public sector
        (βZ/H,ρE,1 < 0) but not the private sector (βZ/H,ρE,1 = 0). Other results are more
        unusual, though: Men are more responsive (for instance, βH,τE,0 = 0.317) to
        changes in marginal employee NICs rates than women (βH,τE,0 = 0.033), which
        contrasts with the typical finding in the literature.33 However, this could partly
        be an artefact of one particular measurement problem we face: our inability to
        observe whether women in our sample are subject to the married women's reduced
        rate of employee NICs (see Section 2.1). This rate has not changed in the same way
        as the standard rates of employee NICs that we model. Measurement error in NICs
        rates may therefore attenuate estimates of responses to employee NICs for women.
        While incidence is initially close to statutory, statistically significant
        coefficients on lagged changes in average net-of-employer-NICs rates suggest that
        employers more than fully bear employer NICs for women and those aged over 50
        after 12–18 months. This could reflect ‘overshifting’ of employer NICs to
        employers, which (as noted in Section 3.1) is possible in labor markets
        characterised by wage bargaining. This is consistent with the fact that older
        workers are more likely to be members of trade unions in the UK, although
        historically women were less likely to be members than men (this reversed around
        the year 2000).34 In contrast, employees seem to more than fully bear employee
        NICs among the over-50s. This is more difficult to rationalise.

     <hss>Summary</hss>

        Overall, while estimates differ quantitatively to some extent across
        specifications and across sub-samples, we find consistent evidence that the
        statutory incidence of NICs matters for their economic effects. In particular: The
        compensated elasticity of hours with respect to the marginal net-of-employee-NICs
        rate is generally positive (βX,τE > 0), while that for employer NICs is generally
        not statistically significantly different from 0. The elasticity of hourly labor
        cost with respect to the average net-of-employee-NICs rate is generally close to
        0, while that for the average net-of-employer-NICs is generally close to −1. Our
        preferred interpretation is that employees respond to NICs by adjusting their
        labor supply on the intensive margin, but that wage stickiness (lasting at least a
        year) means that the statutory incidence of NICs significantly affects their
        impact on behavior and their economic incidence in the short-to-medium term. Our
        decomposition of labor cost into hours and hourly labor costs allows us to rule
        out the possibility that responses to marginal net-of-employee-NICs rates reflect
        increases in wage rates – which is a prediction of some bargaining models of the
        labor market – rather than changes in labor utilisation.

<h>CONCLUSIONS</h>
-----------

In this paper we have estimated the responses of labor cost, hours of work and hourly
labor cost to marginal and average rates of employee and employer SSCs in the UK, using
reforms during the 1980s, 1990s, 2000s and early 2010s as our source of identifying
variation. The existing literature analysing the responsiveness of earnings to SSCs using
micro-data is sparse relative to the voluminous literature on the responses of taxable
income to income tax; this paper helps to fill that gap. Furthermore, by considering
estimated effects in the context of both behavioral responses to SSCs and the (intimately
related) issue of their economic incidence, this paper attempts to help link the ETI and
incidence literatures. Our main specifications include both contemporaneous and lagged
changes in net-of-NICs rates, allowing us to look at the impact of NICs over the first
year or so following a reform, rather than just the immediate impacts over the first 0 to
6 months. And multiple policy reforms provide us with the power to separately identify the
effects of employee and employer NICs. Our estimates suggest that responses to employee
and employer NICs differ significantly. We find that reductions in marginal rates of
employee NICs have positive and statistically significant effects on labor cost, operating
via hours of work. We also find that labor cost falls more than one-for-one when average
employer NICs rates are reduced, but by much less when employee NICs rates are reduced,
with most of the effect (and nearly all of the difference) operating via hourly labor
cost. These findings are robust across specifications based on different instruments,
different sub-periods of analysis, and different sub-groups of employees. We interpret
this as evidence that employees change their hours in response to NICs, but that in the
short- to medium-run at least, the formal incidence of NICs matters for their behavioral
impacts and economic incidence. If employers respond to changes in marginal employer NICs
rates at all, they do so by adjusting the number of employees they hire and/or how they
compensate their employees (things we cannot observe in our data), rather than by
adjusting the hours offered to individual employees. Lehmann et al. (2013) draw similar
conclusions from their analysis of the effects of changes in income tax and employer SSCs
on labor costs in France. But our decomposition of labor cost into hours and hourly labor
costs allows us rule out the possibility that the positive compensated elasticity of labor
cost with respect to marginal employee NICs rate arises via the wage bargaining process
rather than changes in hours of work. Our estimates of the effects of average employee
NICs rates on hours of work suggest that income effects are significant for the wage
earners for whom our elasticities are estimated. We also find that reductions in average
employer NICs rates lead to statistically significant reductions in hours of work. This
cannot be rationalised as an income effect if, as our hourly labor cost regressions imply,
the short-run incidence of employer NICs is on firms. One potential explanation is that a
reduction in average employer NICS rates, holding marginal rates constant, is akin to
providing firms with an extra lump sum per worker: a plausible response by firms could
therefore be to utilise more workers, each working fewer hours. Future work could extend
this analysis in several ways. First, one could consider the effects of income tax and of
means-tested benefits and tax credits. In addition to allowing an assessment of the
impacts of these additional policies, it would also allow for more robust estimation of
the impacts of NICs (by reducing the risk of omitted variable bias). The NESPD, on which
this study is based, does not allow us to estimate the marginal and average tax rates
associated with these parts of the tax and benefit system: they are assessed on broader,
usually family-level, measures of income, rather than individual earnings. To do this in
the UK, one would therefore need to make use of alternative datasets such as the Family
Expenditure Survey which can provide such information, but which also has a smaller sample
size and greater measurement error in earnings than the NESPD. Another possibility would
be to use data from a country with detailed administrative panel data on both individual
earnings and family incomes and composition. Second, it would be worthwhile to examine the
longer-run incidence of SSCs by examining the impact of reforms beyond the first year.
Estimating long-run incidence is more difficult, though, as the potential for other
differential changes in policy/institutions or the economic environment to impact labor
costs is greater, making it more difficult to isolate the effects of SSCs. A third
interesting extension would be to examine the ultimate incidence of SSCs that are not
incident on the individual employee on whose earnings they are levied. For instance, using
matched employee-employer data, if there is firm-level variation in exposure to different
reforms to SSC rates, one could examine whether incidence is shifted on to other employees
in a firm that are not directly affected by particular reforms, or is shifted elsewhere,
such as to shareholders, customers, or suppliers. Where the ultimate economic burden of
SSCs lies can have important implications for not only their distributional effects, but
also for the measurement of the fiscal externalities generated by them.


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  [20] Christopher A. Pissarides. The impact of employment tax cuts on unemployment and wages; the role of unemployment benefits and tax structure. doi:10.1016/S0014-2921(97)00090-1
  [21] Emmanuel Saez, Joel Slemrod, Seth H. Giertz. The elasticity of taxable income with respect to marginal tax rates: A critical review. doi:10.1257/jel.50.1.3
  [23] Caroline E. Weber. Toward obtaining a consistent estimate of the elasticity of taxable income using difference-in-differences. doi:10.1016/j.jpubeco.2014.05.004
<ART>Administrative barriers to trade
================================

Authors: Cecília Hornok, Miklós Koren
DOI: 10.1016/j.jinteco.2015.01.002
Year: 2015  |  Pages: S110-S122
ASJC codes: 2002, 2003
Keywords: Administrative barriers, Customs union, Gravity equation, Trade facilitation

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We build a model of administrative barriers to trade to understand how they affect trade volumes, shipping decisions and welfare. Because administrative costs are incurred with every shipment, exporters have to decide how to break up total trade into individual shipments. Consumers value frequent shipments, because they enable them to consume close to their preferred dates. Hence per-shipment costs create a welfare loss.We derive a gravity equation in our model and show that administrative costs can be expressed as bilateral ad-valorem trade costs. We estimate the ad-valorem equivalent in Spanish shipment-level export data and find it to be large. A 50% reduction in per-shipment costs is equivalent to a 9 percentage point reduction in tariffs. Our model and estimates help explain why policy makers emphasize trade facilitation and why trade within customs unions is larger than trade within free trade areas.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Exporters and importers around the globe face many administrative barriers. They have to
comply with complex regulations, deal with a large amount paperwork, subject their cargo
to frequent inspections, and wait for lengthy customs clearance. Minimizing the burden of
these procedures, “trade facilitation” has been a priority for policymakers from developed
and developing countries alike. In December of 2013, all members of the World Trade
Organization (WTO) have agreed to the Bali Package, the first comprehensive agreement of
the Doha round of negotiations. The main component of the Bali Package is an agreement on
trade facilitation, requiring WTO members to adopt a host of measures streamlining the
customs process, such as pre-arrival processing of shipments, electronic documentation and
payment, and the release of goods prior to the final determination of customs duties,
“[w]ith a view to minimizing the incidence and complexity of import, export, and transit
formalities and to decreasing and simplifying import, export, and transit documentation
requirements […]”1 Why do countries rush to facilitate trade? They hope to increase trade
volumes without endangering government revenues by reducing inefficiencies. In fact,
studies of various trade facilitation measures find that they are associated with larger
trade volumes.2 Even among countries within free trade areas (FTAs), tighter economic
integration and a reduction of administrative barriers often lead to higher trade.3 We
build a model of administrative barriers to trade to understand how they affect trade
volumes, shipping decisions and welfare. A large part of administrative trade barriers are
costs that accrue per each shipment, such as filling in customs declaration and other
forms, or having the cargo inspected by health and sanitary officials. Hornok and Koren
(in press) document that countries with high administrative barriers to importing (as
reported in the Doing Business survey of the World Bank) receive less frequent and larger
shipments. The starting point of our model is hence a tradeoff between administrative
costs and shipping frequency. In the presence of per-shipment administrative costs,
exporters would want to send fewer and larger shipments. However, an exporter waiting to
fill a container before sending it off or choosing a slower transport mode to accommodate
a larger shipment sacrifices timely delivery of goods and risks losing orders to other,
more flexible (e.g., local) suppliers. With infrequent shipments a supplier of such
products can compete only for a fraction of consumers in a foreign market. We first use
our model to derive a modified gravity equation of trade flows, in which administrative
barriers show up as an additional tax on imports. Intuitively, when administrative
barriers are high and shipments are infrequent, customers suffer utility losses that can
be quantified as an ad-valorem tax equivalent. They also substitute towards local products
accordingly. We then show how to measure the welfare losses from administrative barriers
to trade by estimating two key elasticities from the data. First, we need to know the
sensitivity of consumers to timely shipments. This can be recovered from the observed
shipping choices of exporters: if customers are very sensitive to timeliness, firms send
many small shipments. Second, we need to estimate shippers' reaction to administrative
costs. Calculating deadweight losses from the elasticity of consumer and firm behavior to
prices is in the spirit of semi-structural estimation of Harberger (1964), Chetty (2009)
and Arkolakis et al. (2012). In our empirical analysis, we first show that per-shipment
trade costs are sizeable and important for trade flows. We use the Doing Business database
to measure the cost of shipping. Across 161 countries, the average trade shipment was
subject to $3000 shipping cost in 2009. High shipping costs are associated with low
volumes of trade: country pairs at the 25th percentile of per-shipment costs trade 68%
more than country pairs at the 75th percentile. This magnitude is comparable to the trade
creating effect of sharing a common border. Administrative barriers of trade are larger in
poor countries than in rich ones. Doubling the income of an importing country is
associated with a 6% decrease in per-shipment costs. This pattern is consistent with the
fact reported by Waugh (2010) that poor countries have higher trade barriers than rich
ones, without correspondingly higher consumer prices of tradables. In our model,
administrative barriers affect the convenience of imports and hence trade volumes, but not
consumer prices. In addition, we find that administrative costs help explain trade flows
among countries with no preferential trade agreements and even within FTAs, but not within
customs unions. One potential reason for this is that customs unions are subject to much
less administrative barriers than FTAs and our measured administrative costs do not apply.
In fact, this could provide a new explanation for why trade within customs unions is
higher than trade within FTAs.4 Traditionally, the analysis of FTAs relative to customs
unions focused on tariff harmonization, rules of origin and political economy (Krueger,
1997 and Frankel et al., 1997, 1998). We then study how exporters break down trade into
shipments by exploiting shipment-level data for Spain for the period 2006–2012. We find
that countries facing higher administrative barriers receive fewer shipments. This is
similar to the finding of Hornok and Koren (in press). Using our estimated elasticity of
the number of shipments with respect to per-shipment costs, we can calibrate the welfare
effect of these costs. We conduct two counterfactual trade facilitation experiments in the
model. In the first one we reduce per-shipment costs by half. In the model, this is
equivalent to about a 9% reduction in tariffs and results in about a 31% increase in trade
volumes. The second exercise harmonizes administrative barriers so that each country
matches the per-shipment cost of the average country in the top decile of GDP per capita.
Because richer countries have lower trade barriers, this typically involves a reduction in
per shipment costs. The tariff-equivalent effects of this policy vary substantially with
development, being 13% for the lowest income decile and 2% for the highest. Our
counterfactual exercises suggest large trade creating effects of trade facilitation and
large distributional effects from harmonizing administrative barriers. Our emphasis on
shipments as a fundamental unit of trade follows Armenter and Koren (2014), who discuss
the implications of the relatively low number of shipments on empirical models of the
extensive margin of trade. We relate to the recent literature that challenges the
dominance of iceberg trade costs in trade theory, such as Hummels and Skiba (2004) and
Irarrazabal et al. (2013) They argue that a considerable part of trade costs are per unit
costs, which has important implications for trade theory. Per unit trade costs do not
necessarily leave the within-market relative prices and relative demand unaltered, hence,
welfare costs of per unit trade frictions can be larger than those of iceberg costs.5 The
importance of per-shipment trade costs or, in other words, fixed transaction costs has
recently been emphasized by Alessandria et al. (2010). They also argue that per-shipment
costs lead to the lumpiness of trade transactions: firms economize on these costs by
shipping products infrequently and in large shipments and maintaining large inventory
holdings. Per-shipment costs cause frictions of a substantial magnitude (20% tariff
equivalent) mostly due to inventory carrying expenses. We consider our paper complementary
to Alessandria et al. (2010) in that we exploit the cross-country variation in
administrative barriers to show that shippers indeed respond by increasing the lumpiness
of trade. Relative to their work, our focus is on characterizing the welfare consequences
of administrative barriers in a simple-to-calibrate framework. We can do this by
leveraging the semi-structural approach. Our work is most related to Kropf and Sauré
(2014), who build a heterogeneous-firm trade model to study how fixed costs per shipment
affect shipment size. They characterize the size and frequency of shipments as a function
of firm productivity, and also show that aggregate exports follow from firm-level trade
patterns. They then recover shipment costs from the observed shipment sizes, showing that
these imputed costs are large and correlate plausibly with geographic variables and trade
agreements. Given our lack of firm-level data, our model is admittedly simpler, but our
focus here is also different: we want to understand the welfare consequences of
administrative trade costs in a tractable aggregate framework. For this purpose, we derive
a standard gravity equation in our model, and show how our model can be calibrated using a
limited set of aggregate moments. We also offer new evidence on the trade effects of
administrative barriers within and outside customs unions and conduct various
counterfactual experiments.

<h>A MODEL OF THE SHIPPING FREQUENCY OF TRADE</h>
------------------------------------------

This section presents a model that determines the number and timing of shipments to be
sent to a destination market. Sending shipments more frequently is beneficial, because
consumers value timely shipments. Producers engage in monopolistic competition as
consumers value the differentiated products they offer. Each producer can then send
multiple shipments to better satisfy the demands of its consumers. There are J countries,
each hosting an exogenous number of sellers and consumers. A seller can sell to a domestic
consumer at no shipping cost. It can also sell to a foreign destination j, in which case
it has to pay iceberg shipping costs as well as the administrative cost of exporting to
country j. The difference between administrative barriers and other trade costs is that
the former apply for every shipment. We hence model them as per-shipment costs that are
pure waste. We characterize the shipping problem of sellers, and derive a gravity equation
for trade flows between countries. We show that administrative costs act as an ad-valorem
tax on bilateral trade. We then discuss the welfare implications of administrative costs,
deriving a semi-structural formula for consumer surplus in the spirit of Harberger (1964),
Chetty (2009) and Arkolakis et al. (2012).

<hs>  Consumers</hs>
  ~~~~~~~~~

Consumers are willing to consume at a date other than their preferred date, but they incur
a cost doing so. In the spirit of the trade literature, we model the cost of substitution
with an iceberg transaction cost.8 A consumer with preferred date t who consumes one unit
of the good at date s only enjoys e− δ|t − s| effective units. The parameter δ > 0
captures the taste for timeliness.9 Consumers are more willing to purchase at dates that
are closer to their preferred date and they suffer from early and late purchases
symmetrically. Clearly, because of perfect substitution, the consumer will only purchase
the shipment(s) with the closest shipping dates, as adjusted by price, e− δ|t − s|/ps.

<hs>  Exporters</hs>
  ~~~~~~~~~

There is a fixed Mi measure of firms producing in each country i. Because there are no
entry costs, each firm exports to each destination country j.10 Exporters decide how many
shipments to send at what times. Sending a shipment incurs a per-shipment cost of fij.
They then decide how to price their product. Both decisions are done simultaneously by the
firms. The marginal cost of production of supplier ω is constant at c(ω).11 It takes gross
iceberg costs tij > 1 for goods to reach country j from country i. This involves the per-
unit costs of shipping, such as freight charges and insurance (it does not include per-
shipment costs.) The cost-insurance-freight value of a good in country j is hence c(ω)tij.
We abstract from capacity constraints in shipping, that is, any amount can be shipped to
the country at this marginal costs. Because we do not study free entry, we abstract from
entry costs for both production and market access. Net revenue is markup times the
quantity sold to all different types of consumers at different shipping dates. The per-
shipment costs have to be incurred based on the number of shipping dates, which we denote
by nj(ω).12

<hs>  Equilibrium</hs>
  ~~~~~~~~~~~

An equilibrium of this economy is a product price pj(t, ω, s), the number of shipments per
firm nj(ω), and quantity xj(t, ω, s) such that (i) consumer demand maximizes utility, (ii)
prices maximize firm profits given other firms' prices, (iii) shipping frequency maximizes
firm profits conditional on the shipping choices of other firms, and (iv) goods markets
clear. To construct the equilibrium, we move backwards. We first solve the pricing
decision of the firm at given shipping dates. We then show that shipments are going to be
equally spaced throughout the year. Given the revenues the firm is collecting from n
equally spaced and optimally priced shipments, we can solve for the optimal number of
shipments.

     <hss>Pricing</hss>

        Price is a constant markup over the constant marginal cost. Firms may be
        heterogeneous in their marginal cost because of differences in productivity or
        factor prices in their source country. Importantly, a given firm charges the same
        price for each shipment date.

     <hss>Shipping dates</hss>

        Clearly, revenue (4) is concave in |s − t|, the deviation of shipping times from
        optimal. Because of that, the firm would like to keep shipments equally distant
        from all consumers. This implies that shipments will be equally spaced, s2 − s1 =
        s3 − s2 = … = 1/n. The date of the first shipment is indeterminate, and we assume
        that firms randomize across all possible dates uniformly. An equal-spaced shipping
        equilibrium is shown on Fig. 1.

     <hss>Revenue</hss>

        The revenue of a firm is the product of two components: one depending only on
        market size and relative price as in a Krugman model, the other solely a function
        of shipping frequency. The ad-valorem equivalent of infrequent shipping, τ(n), has
        the following properties. It is decreasing in n: the more shipments the firm sends
        the more consumers it can reach at a low utility cost. Because they appreciate the
        close shipping dates, they will perceive this firm as relatively cheap. At the
        extreme, if n → ∞, τ(n) converges to 1, and the firm sells r(ω). From the firm's
        point of view, the demand for timely shipping is fully captured by the function
        τ(n), which acts as an ad-valorem tax on the firm's product. Later we will show
        that this analogy also applies to welfare calculations.

     <hss>Number of shipments</hss>

        It increases in δ (less patient consumers), increases in σ (consumers willing to
        substitute to other firms), increases in Ej/Pj (bigger firms in equilibrium) and
        decreases in fij (costly shipments). The number of shipments only depends on the
        ratio of maximal firm size rj(ω) and per-shipment cost fij. Everything that makes
        the firm larger in a market (large market size, weak competition, low costs of
        production and shipping) increases the optimal frequency of shipments. Large firms
        lose more by not satisfying their customers' need for timeliness and they are
        willing to incur per-shipment costs more frequently. Intuitively, lower per-
        shipment costs also imply more frequent shipments. At the extreme, as fij tends to
        zero, the firm sends instantaneous shipments, nj(ω) → ∞ and τ converges to one.
        The left-hand side of this equation is the absolute value of the elasticity of τ
        with respect to n. The right-hand side is a constant markup times total shipping
        costs paid by the firm (nf), divided by total revenue of the firm. The last
        fraction can hence be thought of as the ad-valorem amount of shipping costs. The
        intuition for this result is that the more elastic τ is with respect to the number
        of shipments, the less willing is the firm to sacrifice revenue with infrequent
        shipments. It will hence send many small shipments, making the ad-valorem amount
        of shipping costs large. We can use this formula to recover the elasticity of τ
        from the data.

     <hss>Trade flows</hss>

        The analysis so far is conditional on firm-level unit costs. To derive aggregate
        trade flows, we need to take a stand on these costs. Because we do not have firm-
        level data, we take the simple view that firms within the same country are
        identical in their cost of production, ci(ω) ≡ ci. An alternative approach,
        pursued by Kropf and Sauré (2014) would be to assume heterogeneous firms with
        Pareto-distributed unit costs. Chaney (2008) and Arkolakis et al. (2012) discuss
        under what conditions such a heterogeneous-firm model leads to a similar gravity
        equation to the one we derive below. This is exactly the gravity equation in
        Anderson and van Wincoop (2003) and Eaton and Kortum (2002), except for the
        additional term τ(nij). Infrequent shipment hence acts as a bilateral trade cost
        between countries. We can use this insight to calculate the magnitude of trade
        losses from administrative barriers.

<h>WELFARE</h>
-------

What is the welfare cost of administrative barriers? Here we calculate how welfare depends
on the choice of shipping frequency. The utility of the representative consumer is a
monotonic function of real income Ej/Pj. We hence need to calculate the income and the
price index faced by the representative consumer. Our gravity equation satisfies
Restriction 3 (CES import demand) of Arkolakis et al. (2012), but not Restriction 2
(constant profit shares) and Restriction 3 (identical elasticity of trade flows to wages
and trade costs). This is because profit net of shipping costs is a nonlinear function of
revenue and trade policy hence also changes the profit to cost ratio of the economy. We
thus cannot use the result of Arkolakis et al. (2012) to characterize welfare across all
equilibria. We can still use a loglinear approximation around the equilibrium to show how
the additional inconvenience from an infinitesimal increase in shipping costs maps into
welfare losses for the consumer. Because we only consider changes to fij when analyzing
welfare, we can treat customer income Ej as fixed as long as j is a small country. In this
case, changes in the profits of exporters in country i do not matter for consumer income
in country j. We can focus on changes to the price index.13 The welfare effect of a change
in per-shipment costs is a weighted average across source countries. The contribution of
country i to this welfare effect is ψij. We use this result in the counterfactual exercise
in Section 5 when we estimate ψij.

<h>EVIDENCE ON ADMINISTRATIVE BARRIERS AND TRADE</h>
---------------------------------------------

We study how administrative barriers affect trade flows. We first estimate a gravity
equation for bilateral trade volumes, including cost of shipping as an additional
bilateral trade cost. We then show how shipping costs affect the number of shipments going
to a country.

<hs>  Data and measurement</hs>
  ~~~~~~~~~~~~~~~~~~~~

We identify administrative costs from the Doing Business survey of the World Bank, from
2006 to 2012 (World Bank, 2014a). Doing Business measures the costs of exporting and
importing a standard containerized cargo, noting the various customs and administrative
procedures, documents, and the time and money they take. Our measure of shipping costs is
the total monetary cost per shipment incurred by the exporter and the importer. Although
not all components of these costs are strictly administrative, these correspond to the
per-shipment cost in our model.14 Table 1 reports the average shipping costs across
countries, broken down by the type of procedure and the direction of trade (export or
import). Taken together, the average trade transaction would be subject to a total of
$3000 cost and a waiting time of 50 days. To study the covariates (though not necessarily
determinants) of administrative barriers, we regress the log total per shipment costs
(including both exporting and importing costs) on a host of country and country-pair
observables. Table 2 reports the results. Administrative barriers tend to be lower for
larger and richer countries that are closer to one another and are members of an FTA. By
far the most variation in administrative barriers is due to the level of development of
the exporter and the importer. Doubling the GDP per capita of an importer is associated
with a 6% decline in per-shipment trade costs. Twice as rich exporters, in turn, have 4%
lower shipping costs. Motivated by this observation, we will study the effects of the
counterfactual policy of reducing administrative barriers to rich-country levels.15 Data
on trade flows comes from the UN Comtrade database (United Nations, 2014). We use
bilateral distance measures and geographical variables from CEPII (Mayer and Zignago
2011), and gross domestic product data from the World Bank (World Bank, 2014b). To
estimate how shipping choices depend on administrative costs, we need information on
shipments. We use the shipment-level export database of the Spanish Agencia Tributaria
(Agencia Tributaria, 2014). This contains information on every single international
shipment leaving Spain. It records the date of shipment, its product code, value and
weight, destination and transit countries, and the specifics of shipping, such as the mode
of transport, the flag of vessel and whether the cargo is containerized. Agencia
Tributaria does not make firm identifiers available, so, even though each shipment is made
by a single firm, we cannot conduct firm-level analysis. Table 3 reports some shipment-
level statistics about Spanish export in 2009. It shows, for selected destinations, the
shipment value of the median product, the number of times it is shipped in a month, and
the number of months it is shipped in a year. Our first observation is that shipments are
relatively large and infrequent. The average shipment size across all importers is $13,234
and the typical product only ships twice a year to the typical destination. This
observation, noted before by Armenter and Koren (2014) and Hornok and Koren (in press),
motivated us to model shipments as infrequently spread through time. We also find that
countries with lower per-shipment costs receive smaller and more frequent shipments. In
our model, a shipment can only contain a single type of product from a single firm. In
practice, shipments may be consolidated. Multiproduct firms may send different products or
freight forwarders may send cargo of different firms in the same shipment. To check how
important this model restriction is, we explored the bundling of shipments. For this
exercise, we define a shipment based on shipping characteristics alone (such as date,
final and transit country, vessel, containerization), while ignoring information on the
product or its value. The vast majority, close to 60%, of such shipments contains only a
single product item. We hence view the single-product, single-firm approximation of our
model as empirically relevant. In order to differentiate customs unions from free trade
areas, we use the May 2013 version of the database created by Baier and Bergstrand (2007)
to measure economic integration agreements. Because that data ends in 2005 and Doing
Business starts in 2006, we use the year 2006 in our estimation of trade volumes.

<hs>  Trade volumes</hs>
  ~~~~~~~~~~~~~

We first estimate a gravity equation of bilateral imports. We are interested in the trade-
creating effect of customs unions relative to free trade areas, as well as the effects of
per-shipment costs. Imports from country i to country j depend on an FTA and a customs
union dummy, per-shipment costs, as well as standard gravity control variables. Note that
fij is the sum of export-specific costs in country i and import-specific costs in country
j. The unilateral control variables include total nominal GDP, GDP per capita in PPP terms
(World Bank, 2014b), an indicator for whether the country is an island, and an indicator
for its continent (CEPII GeoDist16). Bilateral controls include distance, adjacency,
former colonial status, indicators for common language, common currency and common legal
origins (CEPII GeoDist and Gravity17) and average bilateral tariff rate (CEPII MacMap18).
We also control for whether one or both country is in the European Union, because within-
EU trade data is collected differently.19 Table 4 reports the results. All specifications
are estimated by ordinary least squares (OLS). Columns 1 through 2 are estimated on the
full sample of 178 exporter countries and 148 importer countries. The specifications vary
by the degree of economic integration of the country pairs. We include an FTA and a
customs union dummy, as well as our measure of shipping costs. The omitted category of
economic integration includes country pairs with no trade agreement, or only preferential
trade agreements short of an FTA. All standard gravity variables have the expected sign
and magnitude. As column 1 shows, countries in FTAs trade much more with one another than
countries outside. An FTA is associated with a more than two-fold increase in trade. We
separate customs unions from FTAs. Since all customs unions are also FTAs, the estimated
effect of a customs union is in addition to the effect of being in an FTA. That is,
customs unions are associated with a 44% increase in trade relative to FTAs.20 This is
consistent with the model and the fact that customs unions require much less
administration than FTAs. Column 2 reports the elasticity of trade volumes with respect to
per-shipment cost to be strongly negative at − 1.06. The interquartile range of per-
shipment costs is $1900 to $3100. This implies that country pairs at the 25th percentile
of shipping costs trade 68% more than country pairs at the 75th percentile.21 What is the
relationship between administrative costs, FTAs and customs unions? To answer this
question, we break the sample into three. Column 3 includes country pairs that are not
members of an FTA. Column 4 includes country pairs that are in an FTA but not in a customs
union. Column 5 includes members of customs unions. We are interested in how the effect of
shipping costs varies across these samples. Since the Doing Business survey asks about a
standard cargo, it does not allow for the special administrative provisions of FTAs and
customs unions. We find that the negative effect of per-shipment cost is strong among
countries outside of FTAs. The effect is similar among FTA members. The negative effect of
shipping costs disappears for customs union members. Indeed, for these country pairs, much
of the shipping costs do not apply, as there is no customs clearance and documentation
needs are much reduced. Column 6 reports a regression in which we interact shipping cost
with FTA and customs union indicators. This is different from the regressions on the three
subsamples in that other variables are restricted to have the same coefficient. Again, we
see large negative association of shipping costs with trade for non-FTA members, somewhat
smaller effects for FTA members, and the effect disappears for customs unions. The
differences between the three groups are highly significant.

<hs>  Shipments</hs>
  ~~~~~~~~~

We then turn to see how exporters break down total trade into shipments. We use shipment-
level export data from Spain for the period 2006–2012. We identify the number of shipments
nij as the total number of shipments going from Spain to country j in given year. One
drawback of the Spanish data is that it contains no firm identifiers. We thus cannot
calculate the number of shipments per firm, so we use the total number instead. Although
admittedly a limitation, this measure is consistent with the model, where all firms are
symmetric, and the total number of shipments Nij = Minij is just a constant multiple of
the number of shipments per firm. Table 5 reports the estimates. Because reporting
standards are different for intra-EU trade, we only include non-EU destinations. Column 1
reports a simple OLS estimate for the 131 non-EU destinations. Countries with higher per-
shipment cost receive significantly fewer shipments, with an elasticity of − 1.34. The
interquartile range of per-shipment costs for non-EU destinations is $2000 to $3000. A
country with $2000 per-shipment costs receives 72% more shipments from Spain than a
country with $3000 costs. Column 2 reports a specification with destination fixed effects.
Such fixed effects can soak up any time-invariant heterogeneity across countries and their
relation to Spain. (This is why the gravity variables are omitted.) The coefficient of
per-shipment costs is still negative but no longer significant, with a p-value of 0.235.22
The fixed effect estimate is very noisy because there is little time-series variation in
administrative costs. An analysis of variance reveals that 91% of the variation in log
shipping cost is soaked by up destination country dummies. An additional 5% can be
attributed to common time dummies, leaving about 4% idiosyncratic time variation. In
column 3 we report a random effect specification, which allows for time-invariant
heterogeneity across countries, but restricts these error terms to be orthogonal to
explanatory variables and to have a normal distribution. Given these restrictions, the
random effect estimator uses both cross-section and time-series variation. The estimated
elasticity of the number of shipments with respect to shipping costs is − 0.764. Our
preferred estimate of this elasticity is the more conservative − 0.451. We will use this
estimate in the baseline counterfactual exercise, and explore sensitivity to other values.
In Hornok and Koren (in press), we have estimated product-level regressions to determine
the elasticity of the number of shipments and the average shipment size with respect to
per-shipment costs. Countries with higher per-shipment import costs receive fewer and
larger shipments from both the U.S. and Spain. The elasticity of the number of shipments
is between − 0.262 and − 0.104.23 Our estimates are larger. One possible explanation is
that there are many zero trade flows at the product level, which biases a log-linear
estimation. Missing trade is not an issue at the country level with a large exporting
country such as Spain. Table 5 of Hornok and Koren (in press) also shows that shipments
are spread throughout the year: countries with high per-shipment cost receive shipments in
fewer months. These empirical patterns motivated our model. We also conducted an empirical
analysis of the margins through which exporters change their shipping frequency. Simply
put, they may (i) send more of the same good in larger shipments, (ii) pick slower modes
of transport that allow for larger shipments and (iii) send bulkier products instead of
small products. We do an index-number analysis to decompose the aggregate response into
these channels. The results are reported in Appendix C. The main results are that shipping
frequency is negatively associated with administrative costs even after controlling for
mode of shipping, and that the mode itself does not vary significantly with administrative
barriers.

<h>THE EFFECTS OF A REDUCTION IN ADMINISTRATIVE COSTS</h>
--------------------------------------------------

To quantify the effects of administrative costs in the model, we conduct two simple
counterfactual exercises. In the first trade facilitation scenario, we reduce per-shipment
costs fij by half. The second exercise exploits the cross-country variation in
administrative costs. We change the administrative cost of each country to that of the
average country in the top income decile. Because poorer countries have higher shipping
costs, this scenario affects them more. The average import cost in the top income decile
is $942, whereas the average export cost is $913. As seen from Propositions 2 and 3, both
the trade volume and the welfare effects are as if bilateral tariffs changed. We hence
only need to calculate the tariff equivalent changes, ψij. We can only do this for the
trade relations of Spain, because we need shipment-level data to calibrate the ad-valorem
equivalent of per-shipment costs. Because of this data limitation and because our semi-
structural approach only applies locally, the counterfactual exercises below should be
understood as partial equilibrium changes. More specifically, we do not study the effect
of the trade facilitation reform on firm profits and the potential spillovers across
countries. We can however, characterize changes in consumer surplus and changes in
bilateral trade volumes as long as the trade policy changes are small. To calculate ψij,
we need to know σ. Following Simonovska and Waugh (2014), we calibrate σ = 4.1. This means
that a 1% increase in ad-valorem trade costs reduces trade by σ − 1 = 3.1%. It also
implies a 32% markup. We also report results with the estimates of Eaton and Kortum
(2002), σ = 8.2. Table 6 reports the average tariff equivalent effects of reducing fij
across the ten income deciles. The first column reports the average per-shipment cost in
the income decile. Consistent with the evidence presented in Table 2, poorer countries
have higher shipping costs. The second column reports the effects of reducing shipping
costs by 50%. For example, for the lowest income decile, such a policy would be equivalent
to an 11.6% decline in tariffs, whereas for the 9th decile, this would be equivalent to a
5.2% tariff decline. The effects are heterogeneous, because the effect of a shipping cost
reduction on the import price index is not linear (recall Proposition 3). Countries with
large per-shipment costs enjoy a bigger gain from a 50% reduction. The third column
reports the tariff equivalent effect of setting each administrative cost to the average of
the top income decile. This effect has a clear tendency with income per capita. Countries
in the poorest decile see an effect equivalent to a 13.4% tariff reduction, whereas the
average effect for countries in the 9th decile is 1.5% (note that even importers in the
top decile gain from Spain reducing its somewhat higher-than-average shipping costs.) For
comparison, the last column of Table 6 shows the average bilateral tariff rate with
respect to Spain. Recall that only non-EU countries are included in this exercise, hence,
even for rich countries, the tariffs are substantial. There is much less variation in
statutory tariff rates across income groups than in the tariff-equivalent effects of
administrative barriers. Hence a trade facilitation reform equalizing administrative
barriers offers a stronger force for convergence than a tariff harmonization reform.

<hs>  Alternative calibrations</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~

Table 7 reports the average tariff-equivalent effects across non-EU countries for
alternative calibrations for the shipment elasticity and the elasticity of substitution.
Reducing per-shipment costs by half is equivalent to reducing tariffs by 7.7 to 15.8
percentage points. A larger shipment elasticity (which implies that timeliness is more
important) corresponds to a larger gain from administrative barrier reduction. The gain
does not depend heavily on σ. The average effects are smaller in the scenario where we
match the shipping cost of rich countries, because this corresponds to a smaller than 50%
reduction for most countries. The equivalent tariff reductions range between 3.9 and 7.7%.
Table 8 reports the average percentage increases in bilateral imports from Spain. Given
that Spain is a small trade partner for most of the 131 countries, this exercise ignores
third-country effects. Trade volumes go up dramatically after this reduction in per-
shipment costs, especially for high σ. With σ = 8.2, the trade creating effect of trade
facilitation reform ranges from 31.3 to 148.0%. Even with σ = 4.1, we see a 14.6 to 57.5%
trade increase. These magnitudes are comparable to the trade creating effects of customs
unions (Table 4). There is a wide distribution of the effects across countries, because
they are subject to different per-shipment costs. Fig. 2 plots the tariff equivalent of
the per-shipment cost reduction for the cross-section of non-EU countries. For the bulk of
the countries, the counterfactual trade facilitation reform is equivalent to 0 to 20% age
point reduction in tariffs.

<h>CONCLUSION</h>
----------

We built a model of administrative barriers to trade to understand how they affect trade
volumes, shipping decisions and welfare. Because administrative costs are incurred with
every shipment, exporters have to decide how to break up total trade into individual
shipments. Consumers value frequent shipments, because they enable them to consume close
to their preferred dates. Hence per-shipment costs create a welfare loss. We derived a
gravity equation in our model and showed that administrative costs can be expressed as
bilateral ad-valorem trade costs. We estimated the ad-valorem equivalent in Spanish
shipment-level export data and find it to be large. A 50% reduction in per-shipment costs
is equivalent to a 9 percentage point reduction in tariffs. Our model and estimates help
explain why policy makers emphasize trade facilitation and why trade within customs unions
is larger than trade within free trade areas.


<h>REFERENCES</h>
----------

  [1] Scott L. Baier, Jeffrey H. Bergstrand. Do free trade agreements actually increase members' international trade?. doi:10.1016/j.jinteco.2006.02.005
  [2] Thomas Chaney. Distorted gravity: The intensive and extensive margins of international trade. doi:10.1257/aer.98.4.1707
  [7] Houssein Guimbard, Sébastien Jean, Mondher Mimouni, Xavier Pichot. MAcMap-HS6 2007, an exhaustive and consistent measure of applied protection in 2007
  [11] David Hummels, Alexandre Skiba. Shipping the good apples out? An empirical confirmation of the Alchian-Allen conjecture. doi:10.1086/422562
  [13] Andreas Kropf, Philip Sauré. Fixed costs per shipment. doi:10.1016/j.jinteco.2013.10.003
  [14] Anne O. Krueger. Free trade agreements versus customs unions. doi:10.1016/S0304-3878(97)00032-1
  [16] J. M.C. Santos Silva, Silvana Tenreyro. The log of gravity. doi:10.1162/rest.88.4.641
  [17] Ina Simonovska, Michael E. Waugh. The elasticity of trade: Estimates and evidence. doi:10.1016/j.jinteco.2013.10.001
  [19] Michael E. Waugh. International trade and income differences. doi:10.1257/aer.100.5.2093
  [23] George Alessandria, Joseph P. Kaboski, Virgiliu Midrigan. Inventories, lumpy trade, and large devaluations. doi:10.1257/aer.100.5.2304
  [24] James E. Anderson, Eric Van Wincoop. Gravity with gravitas: A solution to the border puzzle. doi:10.1257/000282803321455214
  [25] Costas Arkolakis, Arnaud Costinot, Andrés Rodríguez-Clare. New trade models, same old gains?. doi:10.1257/aer.102.1.94
  [26] Roc Armenter, Miklós Koren. A balls-and-bins model of trade. doi:10.1257/aer.104.7.2127
  [27] Cecília Hornok, Miklós Koren. Per-shipment costs and the lumpiness of international trade. doi:10.1162/REST_a_00468
<ART>Bequests and heterogeneity in retirement wealth
===============================================

Authors: Mariacristina De Nardi, Fang Yang
DOI: 10.1016/j.euroecorev.2014.09.004
Year: 2014  |  Pages: 182-196
ASJC codes: 2002, 2003
Keywords: Bequest, Earnings shocks, Retirement, Social Security, Wealth inequality

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Households hold vastly heterogeneous amounts of wealth when they reach retirement, and differences in lifetime earnings explain only part of this variation. This paper studies the role of intergenerational transmission of ability, voluntary bequest motives, and the recipiency of accidental and intended bequests (both in terms of timing and size) in generating wealth dispersion at retirement, in the context of a rich quantitative model. Modeling voluntary bequests, and realistically calibrating them, not only generates more wealth dispersion at retirement and reduces the correlation between retirement wealth and lifetime income, but also generates a skewed bequest distribution that is close to the one in the observed data.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Why do U.S. households reach retirement with vastly different wealth levels, even when we
condition on realized lifetime income? Can we construct a model that explains this fact?
What are the important features that help generate this heterogeneity? The answers to
these questions help improve our understanding of the factors affecting savings and thus
help inform many kinds of policy reforms, including taxation and social insurance reforms.
As Heckman et al. (1998) wrote, “It is potentially very dangerous to ‘solve’ problems
whose origins are not well understood.” Our main contribution is to study the role of
intergenerational links, in the form of intergenerational transmission of ability and both
accidental and voluntary bequests, in shaping wealth dispersion at retirement and its
correlation with lifetime income. The aggregate importance of wealth transmitted across
generations calls for an investigation of the impact of these transfers on individual
savings, wealth inequality, and its interaction with earnings shocks over the life cycle.
To do so, we study these elements in the context of a rich, quantitative, overlapping-
generations model with incomplete markets, which features earnings risks and incorporates
the key institutional policies providing public insurance for these risks. The interaction
of risks and insurance, in fact, affects saving motives and, thus, observed wealth
accumulation in an interesting and non-trivial way. Besides voluntary and accidental
bequests and transmission of ability from parents to children, other factors have been
shown to be important to understanding saving behavior and cross-sectional wealth
inequality in the U.S. However, we know little about the effects of these elements on
wealth holdings at retirement. These institutional factors include a government-provided
consumption floor (Hubbard et al., 1995), defined benefit pensions, and a more realistic
modeling of Social Security rules (Scholz et al., 2006). We explicitly model all of these
factors, as they might have important effects directly, but might also interact with the
effects of intergenerational links on savings at retirement and, if not accounted for,
provide a misleading picture of the effects of intergenerational links. In our framework,
after we control for lifetime earnings, wealth differences at retirement arise for the
following two reasons. First, when borrowing constraints prevent households from smoothing
consumption intertemporally, households that differ in the timing of earnings over the
life cycle will have very different wealth levels at retirement. Second, inheritances add
another source of wealth heterogeneity among households with similar lifetime earnings.
Our calibrated bequest motive implies that bequests are a luxury good and thus increases
the desire to leave bequests for households receiving large bequests, thereby increasing
their saving rate and leading to more wealth inequality and less correlation of wealth to
lifetime earnings. Our main finding is that the model with intergenerational links matches
the data well. More specifically, it generates an average of the Gini coefficients for
wealth, after controlling for lifetime income, of 0.53, compared with 0.52 in the data;
and a correlation coefficient between lifetime earnings and retirement wealth of 0.75,
which is a bit higher than in the data (0.62), but lower than in the version of the model
that does not allow for intergenerational links. Adding a modest amount of measurement
error in earnings and wealth further reduces this correlation to 0.71. Removing the
voluntary bequest motive, even in the presence of different assumptions about the receipt
of involuntary bequests, increases the gap between the model and the data. To make this
point, we compare the benchmark model with all intergenerational links, including
voluntary bequests, with two models without voluntary bequest motives, which differ in the
timing and size of accidental inheritances receipt. First, accidental bequests of
different sizes are received at age 50. Second, accidental bequests of different sizes are
randomly received at realistic ages between 35 and 55. The versions of the model without
voluntary bequest motives generate average Gini coefficients for wealth that, controlling
for lifetime income, are 0.46 and 0.46, respectively, which are lower than the 0.52
observed in the data. They also imply a tighter relationship between lifetime earnings and
retirement wealth. More specifically, the correlation coefficients between these variables
are 0.81 and 0.80, respectively, compared with 0.62 in the data. In contrast, as one might
have expected, the intergenerational transmission of earnings ability from parents to
children tends to increase the correlation between wealth and lifetime earnings at
retirement. In fact, the model with bequest motives, but without intergenerational
transfer of productivity, implies a correlation of 0.73, which is lower than the 0.75 in
the benchmark calibration. Without intergenerational transmission of earnings ability, the
distribution of inheritance received is independent of households earnings; this implies
that poorer people tend to receive comparatively larger inheritances, which helps reduce
the correlation coefficient between lifetime earnings and retirement wealth. We also
investigate the distributional effects of means-tested minimum consumption programs in old
age, Social Security, and pensions. Eliminating the realistically calibrated consumption
floor from our benchmark calibration results in the income-poor households having more of
an incentive to save to insure against bad income shocks; this tends to decrease wealth
inequality and generates a lower average Gini coefficient, after controlling for lifetime
income, of 0.49, compared with 0.53 in the benchmark model, while the correlation of
wealth at retirement and permanent income barely changes. Removing private pensions raises
the average wealth of the households in the high earnings deciles, as they save much more
to smooth consumption over their lifetime. As a result, the Gini coefficients decrease a
lot at the higher earnings deciles, and the average of the Gini coefficients across income
deciles drops to 0.49. For the same reason, the correlation coefficient between retirement
wealth and lifetime income increases to 0.79. If, on top of removing private pensions, one
were to switch from a history-dependent Social Security system, the wealth Gini
coefficients for the lower earnings deciles would increase, while the ones for the highest
earners would decrease. On net, the average of the Gini coefficients across income deciles
would barely change, while the correlation coefficient between wealth and lifetime
earnings would increase to 0.82. The most closely related paper to ours is the one by
Hendricks (2007a), who points out the importance of accounting not only for the marginal
distribution of wealth, but also for the joint distribution of wealth and earnings. His
work first documents key features of these data in the Panel Study of Income Dynamics
(PSID) and then studies a life-cycle model in which all households inherit at age 52 and
have no information about these inheritances, which are also not correlated with earnings.
We add to his contribution by introducing transmission of both physical and human capital
across generations. These features, once realistically calibrated, imply that households
receive an inheritance at a random time that is consistent with their parent׳s life
expectancy; and the size and timing of the inheritance is consistent both with their
parents׳ estate and with the distributions of estates left in the U.S. economy. In
addition, due to the luxury voluntary bequest motive coming out of our calibration, people
who either receive high labor incomes or large bequests hold onto more wealth due to a
voluntary bequest motive, which is stronger for richer people, thus generating savings
behavior in old age that is more consistent with the observed data (see De Nardi et al.,
2010). The paper is organized as follows. Section 2 frames our contribution in the context
of the rest of the literature. Section 3 presents the model and the calibration of the
model. Section 4 shows the quantitative results of the benchmark model and investigates
the role of various features of the model. Section 5 concludes.

<h>OTHER RELATED LITERATURE</h>
------------------------

Many authors document that households with similar characteristics, such as lifetime
income, age, and family structure, hold vastly different amounts of wealth at retirement
(see Hurst et al., 1998; Grafova et al., 2006). Hendricks (2007a) shows that the
correlation coefficient between lifetime earnings and wealth at retirement (0.61) is much
less than unity and that substantial wealth differences remain after controlling for
lifetime earnings and age. In fact, the average of the Gini coefficients in wealth at
retirement across lifetime earnings deciles is 0.54, compared with 0.62 in the full
sample. Several economists (for example, Bernheim et al., 2001; Hendricks, 2007a) argue
that these features of the data are inconsistent with most life-cycle models of
consumption-saving behavior and thus constitute a challenge to such theories and their
policy implications. Our goal is to see how close we can get to the observed data once we
allow for a rich model with earnings risk and many features of public insurance, which
also includes intergenerational transmission of physical and human capital across
generations. An extensive literature, both empirical and theoretical, shows that the
transmission of physical and human capital from parents to children is a very important
determinant of households׳ wealth in the aggregate economy (see Kotlikoff et al., 1981;
Gale and Scholz, 1994), and of both wealth and earnings ability over the household׳s life
cycle (see Becker and Tomes, 1979; Hurd and Smith, 2001). As a result, it is also a prime
candidate to investigate retirement savings. This paper also builds on a large literature
that studies the cross-sectional wealth inequality at all ages (see Huggett, 1996;
Quadrini, 2000; Castaneda et al., 2003; De Nardi, 2004, and Cagetti and De Nardi, 2006).
It is also related to studies on retirement saving. Engen et al. (1999, 2005), and Scholz
et al. (2006) study the adequacy of household retirement saving. Those papers abstract
from the intergenerational links of bequests and earnings ability. Gokhale et al. (2001)
abstract from voluntary bequest motives. We assume imperfect altruism in the form of warm
glow and partial inheritability across generations, and we discuss the effects of removing
or changing Social Security on inequality and the correlation of income and wealth at
retirement time. Interesting and complementary work by Fuster (1999) and Fuster et al.
(2003, 2007) assumes perfect altruism across generations and finds that Social Security
programs have important implications for capital accumulation and inequality. Our results
under imperfect altruism are broadly consistent with theirs.

<h>THE MODEL</h>
---------

The model is a discrete-time, incomplete markets, overlapping generations economy with an
infinitely lived government.

<hs>  Demographics, preferences, and labor productivity</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Agents also derive utility from the bequests transferred to their children upon death.
This form of ‘impure’ bequest motive implies that an individual cares about total bequests
left to his/her children, but not about the consumption of his/her children.

<hs>  Calibration</hs>
  ~~~~~~~~~~~

Unless stated otherwise, we report parameters at an annual frequency. Table 1 lists the
parameters that are either taken from other studies or can be solved independently of the
endogenous outcomes of the model. The tax rate on labor income and the contribution rate
to the defined benefit plan, belong to the latter group because, due to the assumption of
exogenous labor supply and retirement decisions, they only depend on the earnings shocks
and the population demographics, which are exogenous to the model. These bend points are
also expressed in terms of average earnings, while the marginal rates are chosen to match
the holding of defined benefit wealth relative to Social Security wealth by lifetime
earning deciles from the Health and Retirement Study (HRS) data set, as reported in Scholz
et al. (2006). Appendix A reports the details of these computations. According to this
formula and consistent with the data, households in the first three lifetime earnings
categories barely have any defined benefit wealth. The discount factor affects saving and
average wealth in the economy. The term ϕ1 measures the strength of bequest motives, thus
we choose the aggregate bequest as a moment. The term ϕ2 reflects the extent to which
bequests are luxury goods, affecting the bequest distribution, especially the high end of
it. To better gauge the quantitative implications of the model, we begin by evaluating the
lifetime earnings implications of the exogenous earnings process that we feed into the
model. Table 3 first reports the percentage of total lifetime earnings earned at selected
percentiles as a fraction of total lifetime earnings generated by the model and then
displays the corresponding figures computed from the PSID observed data. The model
earnings process produces lifetime earnings earned by each lifetime earnings decile that
are very close to those from the PSID data.

<h>NUMERICAL RESULTS</h>
-----------------

We present our numerical results as follows3: The benchmark model, its mechanisms, and its
comparison to the actual data. The role of the bequest motive. The role of
intergenerational transmission of ability. The role of a government-provided consumption
floor. The role of pensions and Social Security. The role of measurement error in both
earnings and wealth in the observed data. In each run, we solve for the dynamic
programming problem and impose budget balance for the government. We then simulate 100,000
households starting from age 20, drawn from the initial distribution of each model. We
define retirement wealth to be the wealth at age 65 and lifetime earnings to be the total
earnings from ages 20 to 60, discounted to age 65.

<hs>  The benchmark model</hs>
  ~~~~~~~~~~~~~~~~~~~

Overall, the benchmark model fits the data well. The first subsection regarding the
benchmark model discusses its fit of the wealth distribution at retirement and of the
wealth distribution across all ages. The second subsection focuses on its implied
correlation between wealth at retirement and lifetime income. The third subsection studies
bequests. The fourth subsection displays the fit of the model for assets and consumption
over the life cycle.

     <hss>Wealth inequality in the benchmark model</hss>

        The top panel of Table 4 reports wealth percentiles at retirement. The first line
        of the top panel refers to data from the PSID4 and shows that, in the data, wealth
        at age 65 is highly unevenly distributed. The richest 1% of people at retirement
        time hold 16% of total retirement wealth, while the richest 5% hold 34% of total
        net worth at retirement time. The second line of the top panel reports the
        corresponding numbers for the benchmark model with intergenerational links and
        bequest motives. That model succeeds in generating a skewed retirement wealth
        distribution that is comparable with the data, with the exception of the top 1% of
        the wealth holdings. The bottom panel of Table 4 reports values of the wealth
        distribution for the whole economy. Wealth for the whole economy is more unevenly
        distributed than wealth at retirement, both in the data and in all models. This
        indicates that a large amount of wealth dispersion in the economy is due to
        differences in age. Here, too, the model fits the data well.

     <hss>Wealth and lifetime earnings in the benchmark model</hss>

        The benchmark model generates a correlation between lifetime earnings and
        retirement wealth of 0.75. While this is a bit higher than the 0.61 in the PSID
        data, the model does generate a good deal of wealth inequality even after
        controlling for lifetime earnings and age. Table 5 illustrates the Gini
        coefficients of retirement wealth for each lifetime earnings decile. We notice two
        important features. First, after controlling for age and lifetime earnings, there
        is still large wealth inequality in the benchmark model: all the Gini coefficients
        are above 0.32. Second, the degree of wealth inequality declines as lifetime
        earnings increase, as is observed in the data. Third, the model does generate
        significant wealth inequality conditional on permanent income. In fact, the
        average of the Gini coefficients across permanent income quantiles turns out to be
        0.53 in the model and 0.54 in the data. To better gauge the amount of wealth
        dispersion at retirement generated by the benchmark model, Fig. 2 compares the
        retirement wealth distributions for the 2nd, 5th, and 9th lifetime earnings
        deciles in the model with those in the PSID. The model successfully replicates the
        fact that households with similar lifetime earnings hold diverse amounts of
        wealth. At each lifetime earnings decile, households in the lower wealth deciles
        hold very little wealth, while households in the higher wealth deciles hold much
        more wealth. Compared with the data, the model matches especially well for the
        households in the middle deciles of the income distribution, while it overstates
        the high wealth percentiles at the 2nd earnings decile and the low wealth
        percentiles at the 9th earnings decile.

     <hss>Bequests in the benchmark model</hss>

        In the benchmark model, retirement wealth inequality arises among households with
        similar lifetime earnings because households differ in the timing of earnings over
        the life cycle and in the amount and timing of inheritances received. Let us now
        turn to the effects of bequest and inheritance heterogeneity on retirement wealth
        heterogeneity. The model with intergenerational links of bequests and earnings
        ability endogenously generates differences in the timing and amount of
        inheritances. To see how large the variation in inheritances is, Table 6 reports
        values for the discounted lifetime inheritance distribution. In the PSID,
        inheritances are highly unevenly distributed, with a Gini coefficient of 0.89, and
        50% of the households receive very little or no inheritance. The top 1% of the
        households receive 35% of all the inheritances. The model generates a skewed
        inheritance distribution that is comparable with the one in the data, with the
        exception of its top 1%. Treating bequests as luxury goods and modeling the
        transmission of earnings ability across generations are essential to match the
        observed skewness in the inheritance distribution. Several modeling choices and
        aspects of the calibration are important in generating this result. First, the
        marginal utility of leaving a bequest is finite at zero bequests, which helps us
        to generate a large fraction of households receiving no inheritances. Second, some
        large inheritances are transmitted across generations because of the voluntary
        bequest motive to hold onto assets if alive at a very old age. Given our
        calibration, the marginal utility of leaving zero bequests is 0.8027. The average
        bequest during our model period, which is five years long, is 0.0140, and the
        average consumption during our model period is 0.3473. Thus, the marginal utility
        of leaving the average bequest is 0.8017, while the marginal utility of average
        consumption is given by 4.8859. Hence, for the person consuming the average
        consumption amount, the marginal utility of consumption is much higher than the
        marginal utility of leaving even a small bequest. However, because the marginal
        utility of bequests declines more slowly than the marginal utility of consumption,
        the richest households have strong bequest motives to save in order to leave some
        assets to their children, even when they are very old. Moreover, in the presence
        of a positive correlation between parents׳ and children׳s earnings, children are
        more likely to be earnings-rich and to receive a large inheritance and thus tend
        to save to leave more wealth to their offspring, hence generating a skewed
        inheritance distribution. Table 7 shows the fraction of lifetime inheritance
        received by households in each lifetime earnings decile. In the PSID, there is a
        positive correlation between lifetime inheritance and lifetime earnings. The
        benchmark model generates an increasing relation between inheritance and lifetime
        earnings. Modeling the transmission of earnings ability across generations and a
        highly correlated lifetime earnings process is key in generating this pattern. The
        monotonicity relation is weaker in the data. This might be due to the fact that in
        reality, individuals differ by numbers of siblings and marital status and each
        married couple might receive inheritances multiple times. More inheritances at the
        lowest earnings decile might help the model to generate less correlation between
        retirement wealth and earnings. Interestingly, assuming that the parent׳s
        productivity and his child׳s initial productivity are perfectly correlated
        increases the discrepancies between the fraction of inheritances received by each
        lifetime earnings decile in the model and the data. The reason is that higher
        intergenerational persistence in productivity generates a stronger positive
        correlation between lifetime inheritance and lifetime earnings. As is shown in
        Table 7, this implies that the fraction of inheritances received by the lowest two
        earnings deciles is only 4.7%, compared with 14% in the data and 10% in the
        benchmark model. We now turn to the effects of inheritance heterogeneity on
        retirement wealth in the benchmark model. The upper panel in Table 8 shows extra
        wealth holding at selected percentiles among those who did inherit, compared with
        those who did not. At each earnings decile, those who never inherited hold less
        wealth than those who have inherited, and the difference increases as the wealth
        percentile increases. The reason is, with operative bequest motives, those who
        have inherited hold a large part of the inheritances at retirement. The top panel
        of this table thus documents the role of bequest receipt on savings by earnings
        and wealth decile. The bottom part of the table, labeled “Random inher. at age 50”
        changes the distribution of inheritances and studies its effects on savings; this
        exercise highlights that the extra wealth holdings among those who have inherited
        are much smaller in the random bequest model than in the benchmark model with
        bequest motives.

     <hss>Consumption and wealth accumulation over the life cycle</hss>

        The goal of this subsection is to show that our benchmark calibrated model can
        also generate the life-cycle profiles of asset holdings and consumption observed
        from the U.S. data. Fig. 3 displays the life-cycle profiles of average assets and
        consumption for both the model and actual data. Both consumption and wealth are
        expressed as a fraction of annual output per capita and are scaled so that the
        data and model coincide at age 55. The consumption data is expenditure and comes
        from Dotsey et al. (2012). The fit of the model is good, and in particular, the
        model generates a hump-shaped consumption profile. The wealth data comes from Cho
        (2012). Here, the model also does a good job of matching the hump-shaped profile
        of wealth accumulation and the relatively slow decumulation after retirement,
        although the model understates the retirement peak and predicts more decumulation
        than the data, despite the presence of a bequest motive.

<hs>  The role of the bequest motive</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

To isolate the role of the bequest motive from the distribution of inheritances, we
compute two versions of the model without bequest motives in which the inheritance
distribution is exogenously taken from the data (see Appendix B for more details): All 50
year olds receive an inheritance of random size (taken from the data), whose size is
uncorrelated with their earnings at age 50, as in Hendricks (2007a). The timing of
inheritance receipt is random and consistent with the data. Table 9 reports several
measures of inequality for the PSID data and the model-generated data in various versions
of the model. The benchmark model with intergenerational links and bequest motives
generates a skewed wealth distribution comparable with the one in the data. In contrast,
the two models without intergenerational links and bequest motives generate much less
wealth concentration than in the observed data. In the model with random bequests that are
received at age 50, the correlation coefficient between lifetime earnings and retirement
wealth and the mean Gini coefficient are farther away from the data (see Table 10)
compared with the benchmark model, thus pointing out that a bequest motive is needed for
those who have received large inheritances to hold a significant portion of them by the
time retirement comes around. In the benchmark model, in fact, households hold onto more
wealth due to operative bequest motives, and this generates more heterogeneity in
retirement wealth for given lifetime earnings. As we have seen in Table 8, the extra
wealth holdings among those who have inherited are much smaller in the random bequest
model than in the benchmark model with bequest motives. Table 10 also shows that making
the timing of bequest receipt more realistic further weakens the relationship between
lifetime earnings and retirement wealth: a borrowing-constrained household that receives
an inheritance earlier consumes more of it and holds onto less wealth at retirement than
an otherwise identical household that receives an inheritance later. However, the
quantitative effect of this factor is very small.

<hs>  The role of intergenerational transmission of ability</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

To study the interaction of bequest motives and intergenerational transmission of ability,
we keep the bequest motive, but we change the intergenerational persistence in earnings,
which in turn endogenously changes the distribution of inheritance. In particular, if
there is no intergenerational link of earnings, inheritances are evenly distributed by
lifetime earnings decile. More generally, higher intergenerational persistence of earnings
ability leads to more wealth accumulation across generations and increases wealth
inequality, as more productive parents save more to leave bequests and have more
productive children, who in turn also save more to share their wealth with their
descendants.

<hs>  The role of the government-provided consumption floor</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Table 11 shows that setting the government-provided consumption floor to zero reduces the
mean Gini by 0.04 to 0.49, because a means-tested minimum consumption guarantee provides
strong incentives for low-income individuals not to save. Due to the persistence of the
earnings process, those low-income households are more concentrated in low lifetime-
earnings deciles. Table 12 shows that without a consumption floor, the Gini coefficients
decrease a lot at the lowest three earnings deciles, since there are fewer poor households
in those deciles. When the consumption floor is removed, the government adjusts the tax
rate on labor to balance its budget. As a result of this change, the wealth Gini
coefficients in the higher income deciles barely change, because the households in those
deciles are too rich to qualify for a consumption-floor transfer. In addition, the change
in the labor tax needed to rebalance the government budget is very small, because the
government outlays due to the consumption floor are very small.

<hs>  The role of pensions and Social Security</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Tables 11 and 12 show that eliminating pension benefits raises the correlation coefficient
between lifetime income and retirement wealth substantially, because it raises average
wealth for households in the high earnings deciles. Compared with the benchmark model with
pensions, the Gini coefficients decrease a lot at the highest five earnings deciles, since
these households now increase saving for retirement. We then further eliminate any kind of
Social Security payments (in addition to removing pension benefits). The fact that the
mean Gini in Table 11 is the same in the benchmark model and in the model without Social
Security and pension hides substantial changes in the Gini coefficient by lifetime
earnings deciles. Table 12 shows that the Gini coefficients at the lower earnings deciles
increase: wealthy households increase savings while poor households do not increase their
saving, allowing them to qualify for the government-provided consumption floor. The Gini
coefficients at the higher earnings deciles decrease since poor households, who are not
likely to qualify for the government-provided consumption floor, increase saving
relatively more than rich households. This comparison shows that Social Security programs
have important implications for inequality. We provide further evidence in Table 13.
Without pensions and Social Security, the Gini coefficient for the retirees at age 65 is
much lower. As an additional test, after eliminating Social Security payments, we give the
same Social Security payment to all retirees, in addition to removing private pensions. As
a result of this change, the resulting Social Security payment to all retirees, determined
from the government׳s budget balance, is large enough that no retiree qualifies for a
minimum consumption-floor transfer anymore. This experiment decreases the Gini
coefficients at the lower earnings deciles because rich households reduce saving while
poor households, holding no wealth before the experiment, do not reduce saving. The Gini
coefficients at the higher earnings deciles increase, because the poor households decrease
saving relatively more than the rich households.

<hs>  The role of measurement error in income and wealth</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The observed log wealth at age 65 follows Adding a small amount of measurement error
reduces the correlation coefficient from 0.75 in the benchmark model to 0.71. The mean
Gini coefficient of retirement wealth is slightly higher (0.55) than that in the benchmark
(0.53). The reason is that adding random noise in earnings affects Gini coefficients only
when enough agents are regrouped into other deciles. Given the wide range of earnings in
each decile, not many agents are regrouped.

<h>CONCLUSIONS</h>
-----------

Empirical studies using micro data find that there is large heterogeneity in retirement
wealth among households with similar lifetime earnings and raise doubts about the ability
of a standard life-cycle model of saving behavior to reproduce the observed facts. We use
an incomplete-market life-cycle model with intergenerational links of bequests and
earnings ability, a government-provided consumption floor, a history-dependent Social
Security system, and a defined benefit pension. We show that this model with earnings
heterogeneity and inheritance heterogeneity generates a substantial amount of
heterogeneity in retirement wealth for given lifetime earnings. This suggests that a
properly specified life-cycle model with bequest motives, consumption floor, and Social
Security pensions captures the fundamental determinants of households saving and wealth
accumulation. This framework might shed light on the effects of policy reforms that affect
saving. We show that government-provided minimum consumption, pensions, and Social
Security have very different distributional effects. In a separate paper, Yang (2013)
studies the consequences of eliminating Social Security in a similar environment to the
one constructed in this paper and finds that the presence of bequest motives reduces life-
cycle saving and thus reduces the gains from Social Security reform. We have assumed that
households are ex-ante identical. Interesting directions for future work include allowing
for heterogeneity in wealth holdings by education (Hubbard et al., 1995; Cagetti, 2003)
and by marital status (Cubeddu and Rios-Rull, 2003 and Guner and Knowles, 2007). Other
interesting extensions include allowing for heterogeneity in preferences (Krusell and
Smith, 1998; Samwick, 1998; Hendricks, 2007b) and in self-control (Ameriks et al., 2007),
in number of children (Scholz and Seshadri, 2007), in rates of return (Guvenen, 2006), and
in health expenditures (De Nardi et al., 2010).


<h>REFERENCES</h>
----------

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<ART>Co-dependence of extreme events in high frequency FX returns
============================================================

Authors: Arnold Polanski, Evarist Stoja
DOI: 10.1016/j.jimonfin.2014.02.001
Year: 2014  |  Pages: 164-178
ASJC codes: 2002, 2003
Keywords: Dependence in risk, Distributional characteristics, Extreme risk assessment, High frequency returns, Multidimensional risk, Multidimensional value at risk

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

In this paper, we investigate extreme events in high frequency, multivariate FX returns within a purposely built framework. We generalize univariate tests and concepts to multidimensional settings and employ these novel techniques for parametric and nonparametric analysis. In particular, we investigate and quantify the co-dependence of cross-sectional and intertemporal extreme events. We find evidence of the cubic law of extreme returns, their increasing and asymmetric dependence and of the scaling property of extreme risk in joint symmetric tails. © 2014 The Authors.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Elliptical distribution of asset returns is a convenient assumption in finance that allows
for numerous applications including risk management, asset and option pricing and
portfolio decisions. In particular, the standard practice with many risky assets is to
assume that the density is multinormal with perhaps a time-varying covariance matrix (see
Diebold et al., 1999). However, Leon et al. (2009), inter alia, find that joint normality
is not supported by empirical evidence. Moreover, correlation – the standard measure of
dependence in the multivariate context – is only a measure of linear dependence and
suffers from a number of limitations (see Embrechts et al., 2002). For example, Patton
(2004) argues that the dependence between assets is stronger during market downturns than
during market upturns and here we find that the probability of extreme co-events varies
over time. These deficiencies are compounded in the covariance measure – an essential
input in many financial applications including hedging, portfolio selection and systematic
risk. While there is a natural interest in the joint density of asset returns, in some
cases a more focused approach is required. Since the density's interior characterizes
small day-to-day disturbances, it may be of substantially less concern to financial
institutions, managers and regulators than the tail behaviour. For this reason, attention
has recently shifted to exceedance measures that account for the expected magnitude of
large movements in the underlying variables of interest such as stock returns, interest or
exchange rates and changes in energy prices and GDP (see, for example, Longin and Solnik,
2001; Butler and Joaquin, 2002; Bae et al., 2003). In particular, Berkowitz (2001)
proposes a censored likelihood test, in which the observations not falling into the
negative tail of the distribution are truncated. While in the univariate setting, the
tails of financial processes have been studied at length (see, for example, Adler et al.,
1998), the literature on multivariate tail analysis is still in its infancy. Employing
results from the multivariate Extreme Value Theory (EVT), Hsing et al. (2004) fit specific
copulas on the bivariate densities (see also Jondeau and Rockinger, 2006; Brodin and
Kluppelberg, 2010; Ning, 2010). Then, employing coefficients inherent in these copulas,
they examine the dependence between returns in the tails. However, recent attempts to
generalise this framework to the multivariate case turned out to be technically and
computationally demanding (see, for example, Aas et al., 2009; see also Diebold et al.,
2000 for some commonsense caveats to uncritical use of EVT). In the theoretical part of
this study, we develop novel techniques tailored to multidimensional data. The proposed
techniques employ a natural generalization of the VaR concept. Multidimensional Value at
Risk (MVaR) is the region of the intersection of univariate VaRs with a nominal
probability mass under a given density function. MVaR is defined by a single cut-off value
and a directional vector. Despite its conceptual simplicity, MVaR is a versatile framework
that allows for simple testing of the tails as well as the overall accuracy of a
multidimensional density forecast (MDF). Moreover, it is straightforward in this framework
to examine extreme co-events and to evaluate dependence in risk. In the empirical part of
this paper, we illustrate the forecast evaluation technique by investigating two of the
most widely used elliptical distribution functions to approximate the empirical joint
distribution of (high frequency) FX returns overall and in the tails. Using a rich set of
synchronized returns, we examine further the co-dependence among FX returns in the tails.
We analyse and quantify both, cross-sectional and intertemporal dependence of the extreme
returns. Our empirical study covers several return frequencies providing a rich picture of
FX (extreme) returns. Further, to the best of our knowledge, this is the first study to
investigate and present clear evidence of the scaling law for multivariate extreme
returns. This is important because the tails of a fat-tailed distribution are invariant
under addition although the distribution as a whole may vary according to temporal
aggregation (Feller, 1971). For instance, if daily returns are i.i.d. t-distributed, then
the central limit law implies that weekly returns converge to the normal distribution.
However, the tails of the weekly return distribution behave like the tails of the daily
returns with the same tail index. The outline of the remainder of this paper is as
follows. In Section 2, we discuss the concept of MVaR, its accuracy evaluation and
dependence in risk. This section contains also a short discussion of the policy and
practical significance of the MVaR framework. Section 3 summarises the high frequency FX
dataset employed and presents the results of our empirical studies. Finally, Section 4
summarises the main findings and offers some concluding remarks.

<h>THEORETICAL FRAMEWORK</h>
---------------------

In this section, we develop a formal framework for investigating distributional
characteristics and co-dependence of multidimensional variables.

<hs>  Joint density tails</hs>
  ~~~~~~~~~~~~~~~~~~~

Fig. 1 illustrates a JDT in the two-dimensional space. A proof of property (4) is included
in the Appendix. As we will see in what follows, the above property of projection (3)
allows for a systematic accuracy evaluation of MDFs over the tails and also overall. Note
that there is an infinite number of directional vectors d and hence MVaRs. Statistically,
there may be no reason to prefer one over the others. Economically, however, the
directional vector implicitly defines the proportion of the assets in the portfolio. For
example, the symmetric directional vector d = −(1, …, 1) captures negative events for a
portfolio with equally weighted assets. This vector is of main relevance for an investor
holding such a portfolio.

<hs>  Multidimensional value at risk</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Therefore, if f is the true data generating process, we can identify observations lying in
the extreme tails by simply inspecting their z-scores.

<hs>  Dependence in risk</hs>
  ~~~~~~~~~~~~~~~~~~

Poon et al. (2004) and Hartmann et al. (2010) employ tail dependence coefficients to
examine extreme events in the equity and FX markets, respectively. However, these
coefficients, while theoretically robust, measure only asymptotic dependence between
marginals of a joint distribution (see Heffernan, 2001 for a directory of tail dependence
coefficients). By contrast, the dependence measures, which we propose below as natural
extensions of the MVaR framework, can capture dependence between more complicated events
(e.g., between two disjoint sets of marginals) with vanishing or non-vanishing
probabilities.

<hs>  Some applications of MVaR framework</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The recent financial crisis brought to the forefront of attention systemic risk. Due to
the interconnectivity of the financial institutions, a shock faced by one institution in
the form of an extreme event, increases the probability other financial institutions
experiencing similar extreme events, (see Nijskens and Wagner, 2011). Recently, there has
been increasing concern among researchers, practitioners and regulators over the
evaluation of models of (financial) risk (see, for example, the report on Global Risks
2012 by the World Economic Forum). Moreover, while it is important to have an aggregate
measure of the total risk, often it is also important to know the direct dependence on,
and inter-relationships of, the specific sources of risk. These developments accentuate
the need for modelling and evaluation techniques that are flexible and yet powerful (Lopez
and Saidenberg, 2000). However, while the literature on aggregating the multiple sources
of risk is gaining momentum (see, for example, Rosenberg and Schuermann, 2006), there
appears to be little research into the joint distribution and evaluation of such risks. By
focussing on the joint distribution, the MVaR framework measures not only the risk
inherent to each source but also the co-dependence of these risks. Important innovations
in the derivatives markets include basket and rainbow options whose payoffs depend on the
value of a basket of assets. Pricing basket options is difficult as the underlying
portfolio is a function of the constituent asset prices. There are basically two
approaches to address this issue. The first is by modelling the (unidimensinal)
distribution of the basket value (e.g., Borovkova et al., 2007). The second approach,
which is perhaps more intuitive, is by focusing directly on the joint density of the
basket's constituent assets. For example, Huang and Guo (2009) price basket (Bermudan)
options as a function of the value of the option in each state of the basket's constituent
assets times the joint probability of the assets being in that state. They estimate the
joint probability of each state using copulas. By offering a simple and versatile method
for an efficient evaluation of joint density estimates, MVaR framework is readily adapted
to assess theoretical or empirical probabilities that can then be used for
multidimensional option pricing.

<h>RESULTS</h>
-------

In this section, we present the results of our empirical studies that employ the
techniques discussed in Section 2. The data was provided by Bank of America and covers the
period from 2 January 2001 to 29 December, 2006. It consists of synchronized 1-min
exchange rates for three currencies, EUR, GBP and CHF against the USD (a total of
1,006,544 observations). The FX market operates continuously from 10.00pm GMT on Sunday to
10.00pm GMT on Friday, so there are a total of 1440 observations in each 24-h window while
the market is open. Summary statistics for the three log returns at 8 and 64 min
frequencies are reported in Table 1. For all three series, daily log returns are
leptokurtic but the departure from the normal kurtosis diminishes for lower frequencies.
The ARCH(4) test for up to fourth order serial correlation in squared returns shows that
all three currency return series display significant volatility clustering. All mean
returns are close to zero and there is a strong positive correlation between each pairs of
the series that increases as the frequency decreases.4 The strong positive correlation is
clearly visible in Fig. 4. In the first part of the experiment, we test the accuracy of
two parametric distributions – the multinormal (MN) and the multivariate-t distribution
(MT) – over multivariate tails. Both specifications are time-varying. Below we discuss the
details of the dynamic estimation of the parametric distributions via a multivariate GARCH
model.

<hs>  Multivariate GARCH model and estimation method</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

To obtain forecasts of the time-varying three-dimensional covariance matrix we employ the
simplified GARCH (S-GARCH) model of Harris et al. (2007). Our choice can be explained on
the basis of the ability of this model to handle t-distributed residuals and its ease of
estimation. However, we experimented with other, widely used multivariate GARCH models
such as BEKK and DCC but the estimation did not always converge. Like many other
multivariate GARCH models, the S-GARCH does not guarantee that the conditional variance-
covariance matrix is positive semi-definite. However, for all three pairs, the estimated
correlation coefficients were found to be between −1 and +1 for all observations. We ML-
estimate the S-GARCH parameters (and the degrees of freedom parameter for the
t-distributed residuals) using the entire sample. We then use these estimates to obtain
the one step-ahead forecast of the covariance matrix.

<hs>  Empirical results</hs>
  ~~~~~~~~~~~~~~~~~

First, we focus on the goodness-of-fit test of the MN and MT specifications over JDTs that
are defined by the selected directional vectors and nominal probabilities. To this end, we
compute from the observations in the relevant tails the normalized z-scores and the
corresponding p-values of the uniformity test. The results of the experiment for returns
at 8 min frequency are reported in Table 2. Similar results were obtained at other
frequencies, for which a sufficient number of tail observations was available. While we
strongly reject multinormality for all tested JDTs, there is some support for the
multivariate-t distribution in symmetric tails with probability mass 5 percent or less. As
all p-values for these tails are larger than 5 percent, we would not reject the null that
the corresponding tail observations were drawn from the multivariate-t at this
significance level. The (cumulative) distribution of asset returns has frequently been
assumed to be Gaussian, Lévy or a truncated Lévy distribution, where the tails become
“approximately exponential”. In contrast, Gopikrishnan et al. (1998) find that the asset
return distribution exhibit a strong cubic power-law behaviour which differs from all
three previous models: unlike the Gaussian or the truncated Lévy distribution, it has
diverging higher moments, and unlike the Gaussian or Lévy it is not a stable distribution.
Our results in Table 2 together with our estimate of 2.75 for the degrees of freedom
(i.e., relatively thick tails), can be seen as a generalization of the cubic law for
extreme returns to the multivariate context. However, our tentative evidence of the cubic
law is limited to symmetric tails with probability mass not exceeding 5 percent. For the
intertemporal dependence for EUR/USD exchange rate, i.e., the co-dependence between two
consecutive EUR/USD returns,7 the co-dependence in Table 4 appears to decrease in α and it
is stronger for higher frequencies. The overall significant intertemporal dependence is a
hallmark of volatility clustering and indicates that clustering becomes stronger for more
extreme returns. The patterns emerging from Tables 3 and 4 have been confirmed for other
bi-dimensional tails and frequencies. It appears that the relationship between the CMVaR
and the risk dependence coefficient on the one hand, and alphas on the other, is
relatively consistent and stable across the three tails and in both cross-section and
intertemporal frameworks. The practical implications of these findings seem to be that, at
least for symmetric tails, we can estimate the multidimensional risk at high frequencies
and then, scale this estimate up to match the desired return time interval, which is
generally daily, weekly or monthly.

<h>CONCLUSION</h>
----------

We develop a formal framework for investigating the distributional characteristics of
multivariate variables with a particular focus on the tails. We extend important
unidimensional risk concepts to the multivariate settings and employ these to examine risk
dependence for a rich set of high frequency FX data. Our investigation into the tails of
high frequency multidimensional returns reveals interesting phenomena, such as asymmetry
of dependence in the positive and negative tails, cubic law of extreme multidimensional
returns and risk scaling in the symmetric tails. Generally, MVaR framework seems to be a
versatile approach, which could be applied also in portfolio decisions and to study
systemic risk. We intend to pursue these avenues in future research.


<h>REFERENCES</h>
----------

  [1] Kjersti Aas, Claudia Czado, Arnoldo Frigessi, Henrik Bakken. Pair-copula constructions of multiple dependence. doi:10.1016/j.insmatheco.2007.02.001
  [2] Erik Brodin, Claudia Klüppelberg. Modelling, estimation and visualization of multivariate dependence for high-frequency data. doi:10.1007/978-3-7908-2413-1_15
  [3] K. C. Butler, D. C. Joaquin. Are the gains from international portfolio diversification exaggerated? The influence of downside risk in bear markets. doi:10.1016/S0261-5606(02)00048-7
  [4] Peter F. Christoffersen. Evaluating interval forecasts. doi:10.2307/2527341
  [6] Valentina Corradi, Norman R. Swanson. Chapter 5 Predictive Density Evaluation. doi:10.1016/S1574-0706(05)01005-0
  [7] Alexandra Dias, Paul Embrechts. Modeling exchange rate dependence dynamics at different time horizons. doi:10.1016/j.jimonfin.2010.06.004
  [8] Francis X. Diebold, Jinyong Hahn, Anthony S. Tay. Multivariate density forecast evaluation and calibration in financial risk management: High-frequency returns on foreign exchange. doi:10.1162/003465399558526
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  [13] P. Gopikrishnan, M. Meyer, L. A.N. Amaral, H. E. Stanley. Inverse cubic law for the distribution of stock price variations. doi:10.1007/s100510050292
  [14] Christian Gourieroux, Joann Jasiak. Value at Risk. doi:10.1016/B978-0-444-50897-3.50013-4
  [15] H. A. Hauksson, M. Dacorogna, T. Domenig, U. Mller, G. Samorodnitsky. Multivariate extremes, aggregation and risk estimation. doi:10.1080/713665553
  [16] Richard D.F. Harris, Evarist Stoja, Jon Tucker. A simplified approach to modeling the CO-movement of asset returns. doi:10.1002/fut.20262
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  [21] Shih Feng Huang, Meihui Guo. Valuation of multidimensional Bermudan options. doi:10.1007/978-3-540-69179-2_14
  [22] Eric Jondeau, Michael Rockinger. The Copula-GARCH model of conditional dependencies: An international stock market application. doi:10.1016/j.jimonfin.2006.04.007
  [25] Ángel León, Javier Mencía, Enrique Sentana. Parametric properties of semi-nonparametric distributions, with applications to option valuation. doi:10.1198/jbes.2009.0013
  [26] Jose A. Lopez, Marc R. Saidenberg. Evaluating credit risk models. doi:10.1016/S0378-4266(99)00055-2
  [27] François Longin, Bruno Solnik. Extreme correlation of international equity markets. doi:10.1111/0022-1082.00340
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<ART>Commodity prices and labour market dynamics in small open economies
===================================================================

Authors: Martin Bodenstein, Güneşs Kamber, Christoph Thoenissen
DOI: 10.1016/j.jinteco.2018.09.009
Year: 2018  |  Pages: 170-184
ASJC codes: 2002, 2003
Keywords: Commodity prices, Search and matching unemployment

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We show that a model of an advanced small open economy with exports in commodities and search and matching frictions in the labour market can match the impulse responses from a panel vector autoregression to an identified commodity price shock. Using a minimum distance strategy, we find that international financial risk sharing is low even for advanced small open economies. Moreover, a strong real exchange rate appreciation is key for an unexpected commodity price increase to induce a tightening of labour market conditions in the model that is in line with the empirical evidence. As in the case of technology shocks discussed by Shimer (2005), proper amplification of the commodity price shock requires a high value of the outside option for unemployed agents. However, vacancies and unemployment hardly respond whenever the real exchange rate channel is mute. These findings suggest the relevance of the open economy dimension for the transmission of demand-type shocks to the labour market more generally.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Wealth effects play an important role in the international transmission of shocks and thus
the international business cycle. Corsetti et al. (2008) demonstrate how even under a
technology shock the associated wealth effect can dominate the substitution effect and
induce an appreciation of the terms of trade rather than a depreciation as commonly
argued. In other words, wealth effects, if strong enough, can fundamentally alter the
international transmission mechanism.2 Commodity price shocks are one of the most common
sources of wealth effects. We use the fact that commodity price shocks can be readily
identified in a panel vector autoregression (PVAR) framework to study their effects on
labour market dynamics in a model of an advanced small open economy with exports in
commodities and search and matching frictions. A strong real exchange rate response is key
for the commodity price shock to transmit to the labour market in line with the data.
Small open commodity-exporting economies and the consequences of fluctuations in the
relevant commodity prices are rarely the focus of academic studies. Instead, Mendoza
(1995), Kose (2002), Schmitt-Grohé and Uribe (2018) and many others studied the effects of
exogenous terms of trade shocks on business cycle fluctuations rather than the more
fundamental concept of commodity prices. The assumption of exogenous terms of trade shocks
might be appropriate in the context of developing economies with a small and homogeneous
set of exportable goods. However, for the case of advanced commodity-exporting economies
this assumption fails to account for the differences between the commodities sector and
the non-commodities traded goods sector: improved terms of trade may, for example, reflect
increases in commodity prices or productivity losses in the traded goods sector and may
thus provide no clear signal about output, consumption, or the labour market.
Distinguishing between commodity prices and the terms of trade is not only interesting in
its own right. Given the small and price-insensitive share of employment in the commodity-
producing sector in our sample countries— the share ranges from 2 to 6% of overall
employment— commodity price shocks resemble a pure wealth transfer and are a prime example
of a demand shock. Our panel includes data from Australia, Canada and New Zealand, all of
which are net exporters of commodities with high quality data on unfilled vacancies, hours
worked, and unemployment. In the PVAR, a shock that raises commodity prices expands all
components of GDP, notably consumption and investment, leads the real exchange rate as
well as the terms of trade to appreciate while the trade balance to GDP ratio turns
positive. Furthermore, labour market conditions tighten as evidenced by a drop in the
unemployment rate, an increase in individual hours worked, and a larger number of unfilled
vacancies. Applied to the case of the Great Recession, the estimates suggest that the
collapse in commodity prices accounted for up to one third of the rise in unemployment in
the sample countries. The impulse response functions from the PVAR can be successfully
matched by the theoretical responses from a standard small open economy model with net
exports in commodities and search and matching frictions in the labour market as in
Diamond (1982), Mortensen (1982), and Pissarides (1985). This exercise provides insights
into the transmission of commodity price shocks, the role of international financial
linkages and the empirical performance of the search and matching model. First, even
advanced commodity-exporting economies are far from sharing risk efficiently through
international financial markets. For our model to match the empirical size and dynamics of
the response in the trade balance to GDP ratio and the real exchange rate after a
commodity price shock international financial risk sharing needs to be low in the model.
Moreover, matching the empirical movements in the real exchange rate is essential to
obtain data-congruent movements in unemployment and vacancies. If financial markets were
better used to smooth consumption, or if commodity price shocks were absorbed by
institutional arrangements such a sovereign wealth fund, the real exchange rate response
would be muted to such an extent that the model could not replicate the dynamics of the
labour market.3 Second, commodity price shocks, as well as demand shocks in general,
transmit to the labour market through their impact on the real exchange rate. We show this
by decomposing labour market tightness (the ratio of unfilled vacancies and job searchers)
into a labour productivity channel and an international channel that captures movements in
the real exchange rate. If the economy is closed or if the real exchange rate response to
commodity price shocks is limited, the response of the labour market to demand-type shocks
is small in particular in the near term given that labour productivity adjusts only slowly
and by a small amount to demand-type shocks.4 Third, the reason why it is the real
exchange rate and not the real price of commodities that matters for the transmission of
commodity price shocks lies in the low share of employment in the commodity-producing
sector. A rise in commodity prices must transmit to the non-commodity sector of the
economy to account for the magnitude of the total employment response in the PVAR. In the
model, a positive shock to commodity prices raises domestic demand for non-commodity
goods. The accompanying real appreciation provides an incentive to the producers of non-
commodity goods to post additional job vacancies causing the number of job matches to go
up. As a result, employment in the non-commodity sector of the economy rises, and overall
unemployment falls even if employment in the commodity-producing sector of the economy is
negligible. Fourth, when distinguishing between traded and non-traded goods our analysis
suggests that the countries in our sample suffer from the Dutch disease effect analysed in
Corden and Neary (1982). In this extension, the employment increase caused by higher
commodity prices is always concentrated among the firms in the non-traded goods sector.
Employment in the traded goods sector falls— the Dutch disease effect— for standard
choices of the elasticity of substitution between traded and non-traded goods and the
elasticity of substitution between domestic and foreign traded goods, but it could rise
under less conventional choices. As the model fits the empirical impulse response
functions better under standard values of the substitution elasticities, we feel
comfortable concluding that employment in the domestic traded goods sector falls even
absent quality data on non-traded and traded goods. Finally, commodity price shocks can be
identified with less controversy than technology shocks and have robust implications for
the labour market.5 Small open economies have negligible impact on world commodity prices;
a recursive identification scheme with commodity prices ordered first appears to be a
defensible specification that leads to a yardstick against which to assess the performance
of theoretical models. The analysis of commodity price shocks identifies the amplification
of labour market tightness in the model as potentially insufficient as did Shimer (2005)
for the case of technology shocks. We address this issue through the aforementioned real
exchange rate channel as well as a preference specification that allows for a consumption
differential between employed and unemployed agents which in turn determines the value of
the outside option for the unemployed agents.6

<h>COMMODITY PRICE SHOCKS IN ADVANCED SMALL OPEN ECONOMIES</h>
-------------------------------------------------------

Among developed economies, net exports of commodities are significant only for a small set
of countries. According to the IMF (2012), net exports of commodities account for more
than 30% of total exports in Australia, Iceland, New Zealand and Norway, and around 20% in
Canada. Furthermore, commodity net exports account for 5% to 10% of GDP on average. We
exclude Iceland and Norway from our analysis. For Iceland, data availability is limited
and for Norway, the presence of its sovereign wealth fund significantly alters the
macroeconomic response to a commodity price shock compared to the other countries.

<hs>  Data description</hs>
  ~~~~~~~~~~~~~~~~

We estimate a panel vector autoregression (PVAR) using quarterly data for Australia,
Canada and New Zealand spanning from 1994 Q3 to 2013 Q4.7 For each country, we include a
trade-weighted real commodity price index, expressed in US dollars. Nine country-specific
macroeconomic time series complete the dataset: GDP per capita, consumption per capita,
investment per capita, the unemployment rate, unfilled vacancies, net exports of goods and
services relative to GDP, the real effective exchange rate, the real wage deflated by
consumer prices, and hours worked per capita. With the exception of the unemployment rate
and net exports, the data are transformed into logs. All data are de-trended. For the
baseline PVAR, we subtract a quadratic trend from the data. To assess the importance of
trade in commodities, consider the most important commodity for the three countries in the
sample, based on net exports as reported in the Harvard Atlas of Economic Complexity (2014
data). Iron ores and concentrates account for 33% of Australia's net exports. In Canada
exports of crude oil account for 30% of net exports, while in New Zealand's 24% of net
exports are accounted for by milk concentrates. The countries in our sample may be
considered to be important players in selected commodity markets. For example, Australia
is the world's largest exporter of iron ore. However, Australia's total production of iron
ore is significantly below China's and world production of iron ores. Similarly, New
Zealand's large exports of milk products (24% of net exports are accounted for by milk
concentrates and another 7% by butter) pale in comparison to milk production in India, the
United States, and the European Union. Economic areas with large domestic markets produce
and consume a significantly larger share of commodities, but export less. As we focus on a
country's role across all commodities and we use country-specifictrade-weighted commodity
prices, assuming price taking behaviour in commodity markets for the countries in our
sample appears justified. For all three countries, commodity prices have experienced high
volatility over the sample. Relative to real GDP, commodity prices are between 5 and 21
times more volatile.

<hs>  Estimation strategy</hs>
  ~~~~~~~~~~~~~~~~~~~

The effects of commodity price shocks on the labour market are estimated using a PVAR
approach. As the relevant time series are short, but the countries in our sample
experience commonalities in their economic structure, combing the data across countries
can improve the quality of the coefficient estimates. Furthermore, estimation of a panel
provides a single benchmark for matching the impulse response functions implied by
theoretical models to their empirical counterparts. The factor A(L) ≡ A0 + A1L + A2L2 + …
denotes a lag polynomial where L is the lag operator. The vector ui, t summarises the
mean-zero, serially uncorrelated exogenous shocks with variance-covariance matrix Σu and
μi denotes the country fixed effect. The lag length is set at 2 in our baseline.8 The
prices of the commodities traded by the countries in our sample are determined in the
world markets. Commodity price shocks are identified through a recursive identification
scheme. With commodity prices ordered first in the Cholesky decomposition, country-
specific shocks are ruled out from affecting commodity prices contemporaneously. However,
domestic developments in our sample countries can in principle feed back into the world
market at all other horizons.9

<hs>  Estimation results</hs>
  ~~~~~~~~~~~~~~~~~~

Fig. 1 plots the median impulse responses, the black solid lines, together with the 90%
confidence intervals of the PVAR to a one-standard-deviation increase in commodity prices.
The shock to commodity prices is both hump-shaped and persistent. The median response of
commodity prices indicates a rise by about 6% by the second quarter. Commodity prices
return to trend after 12 quarters. Rising commodity prices lead to a boom in the
commodity-exporting economies. Output, consumption and investment rise on impact. Output
and investment increase gradually and peak at about 0.15% and 0.75%, respectively. The
increase in private consumption reaches 0.12% after two quarters. In line with the
Harberger-Laursen-Metzler prediction, the net exports position improves by as much as 0.3%
of GDP. The measure of the real exchange rate appreciates following an increase in
commodity prices, thus increasing the international purchasing power of domestic
households and firms. Labour market conditions improve on impact and continue to do so
beyond the rise in commodity prices. At its peak, the median response of vacancies reaches
almost 3% and the unemployment rate drops by 10 basis points. CPI deflated real wages
decline on impact but recover quickly, whereas hours worked rise by somewhat less than
0.25% by the third quarter following the shock. To put these magnitudes into perspective,
when applied to the case of the Great Recession, our estimates suggest that the collapse
in commodity prices accounted for up to one third of the overall rise in unemployment in
our sample countries. At that time, broad commodity price indices declined by 30–50% while
the unemployment rates rose by 2.5 percentage points on average. In the working paper
version, Bodenstein et al. (2016), we report a number of robustness checks such as the
impulse responses from PVARs estimated with data transformed by a linear as well as the
Hodrick-Prescott filter. The shape and the magnitude of the impulse response functions
appear robust to the de-trending method. We also examined sensitivity to changes in the
lag length as well as to the assumption of block-exogeneity of commodity prices. In all of
these cases we obtained similar results as under the baseline specification of the PVAR.
In Section 5 we also analyse the case of less aggregated employment data. The effects of
an increase in commodity prices on commodity net exporters mirror those found for
developed countries that are net importers of commodities. For example, Blanchard and Galí
(2007) report that a shock that raises the price of oil unexpectedly leads to a
contraction in economic activity with GDP falling and unemployment rising. As in other
recent studies, commodity price shocks have a significant, yet quantitatively modest
effect on domestic economic activity in countries that are net exporters of commodities.
After adjusting the magnitude of the shock, Pieschacon (2012) finds that for Norway an 8%
increase in the price of oil pushes up private consumption by 0.2%.10 The qualitative
movements and overall magnitudes of the non-labour market variables are also comparable to
those in Schmitt-Grohé and Uribe (2018) for shocks to the terms of trade rather than
commodity prices in less developed economies. These studies, however, do not report
results for labour market variables.

<h>BASELINE MODEL</h>
--------------

We are interested in understanding the economic channels through which a commodity price
increase induces the persistent fall in unemployment and the lasting increases in unfilled
job vacancies, consumption and investment found in the empirical analysis. To this end, we
augment a standard small open economy model with net exports in commodities and search and
matching frictions in the labour market as in Diamond (1982), Mortensen (1982), and
Pissarides (1985)— the DMP framework. Our empirical findings have some immediate
implications for a theoretical model. First, an increase in commodity prices raises the
revenues from commodity exports. If the increase in revenues induces a strong (negative)
wealth effect on the labour supply in the form of hours worked, then employment,
investment, and non-commodity output could contract depending on the importance of capital
and labour in producing commodities in the short-term. Such wealth effects on hours worked
after a commodity shock are ruled out in our framework by specifying preferences as in
Greenwood et al. (1988). Second, the response of the trade balance to GDP ratio suggests
that the countries in our sample are limited in their capacity to share risk in
international financial markets. Under a low supply elasticity for commodities, the
commodity price increase (fall) constitutes a pure wealth transfer to (from) the
commodity-producing country. If financial markets were complete in the sense of Arrow and
Debreu (1954), these transfers would be very small and would have a negligible impact on
the domestic economy. As the salient features of the model are well understood and
documented in the literature, we simply summarise the model equations in Table 1 and
confine our discussion to those aspects of the model germane to our analysis—the DMP
framework and the commodity-producing sector. The households' first order conditions with
respect to consumption, the marginal value of finding a match as well as the definition of
total consumption of working and unemployed households are given in Eqs. (i) to (iv) in
Table 1. The firms' first order conditions and constraints are Eqs. (v) to (x). Trade in
goods and assets is defined in Eqs. (xvii) to (xxiv). The model equations pertaining to
the flow of labour are summarised in Eqs. (xxv) to (xxxii). Finally, Eqs. (xi) to (xvi)
relate to the firms' adjustment cost functions for investment and vacancies. A detailed
model description is found in the working paper version.

<hs>  Commodities</hs>
  ~~~~~~~~~~~

The profits from commodity extraction, πtc = ptcytc, are distributed to the households.
The data suggest that resource-intensive commodity extraction and endogeneity of the
supply response are not of primary importance for our anlaysis. Fig. 2 panel (a) shows the
share of employment in the commodity-producing sector in total employment. This share
ranges from 3% and 6% for the countries in our sample. Moreover, despite large swings in
commodity prices over the sample period, this share has been roughly constant in Australia
and Canada, and it has been gradually falling in New Zealand. In panels (b) and (c), we
examine the employment dynamics in the commodity-producing sector following a commodity
price shock in alternative specifications of the PVAR. Panel (b) displays the impulse
responses when we included both commodity and non-commodity employment as observables in
the PVAR. Following a commodity price shock employment in both the commodity-producing and
the non-commodity sectors increase, but the increase in total employment stems primarily
from the non-commodity sector. Moreover, employment in the non-commodity sector rises
immediately after the shock, whereas employment in the commodity-producing sector only
increases after 2 quarters. If the expansion in total employment was driven by the
commodity-producing sector, timing and magnitude of the responses should be opposite from
what is shown in panel (b). Alternatively, Panel (c) displays the impulse responses when
we included the share of employment in the commodity-producing sector in total employment
as observable in the PVAR. The statistically significant increase of the share of
employment in the commodity-producing sector is negligible (0.02%). Overall, the evidence
portrayed in Fig. 2 suggests that employment in the commodity-producing sector is not a
major source of variation in total employment after a commodity price shock. Other studies
have also argued that changes in the supply of commodities in response to price changes
are slow to occur. Unless sizeable excess capacity persists in the commodity-producing
sector, the supply response is muted. Focussing on oil-producingNorway, Pieschacon (2012)
includes oil production into a structural VAR. The estimated response of oil production
after an oil price shock is small and insignificant. By contrast, the expansion in non-oil
output is highly significant and about 5 to 8 times larger than the expansion in oil
production depending on the horizon. Further back in history, Kindleberger (1973)
documents for the interwar period that overall production of commodities did not contract
significantly despite sharply declining commodity prices. To summarise, with commodity
production being capital-intensive, employing only a small share of the domestic labour
force, and being slow to respond to price shocks empirically, we deem it defensible to
assume that commodity price shocks primarily transmit to the remainder of the economy
through their impact on transfers and thus wealth. Nevertheless, we assess robustness of
this modelling decision in Section 5.

<h>RECONCILING MODEL AND PVAR</h>
--------------------------

We assess the empirical performance of the baseline model using a minimum distance
strategy. In doing so, we distinguish between calibrated and estimated parameters. The
calibrated parameters are listed in the top half of Table 2. The discount factor, β,
implies a real interest rate of 4% per annum. The parameter σ governs the intertemporal
elasticity of substitution and is set at 1.1. The share of capital in the production
function, α, is 0.33, the depreciation rate, δ, is 2.5% per quarter. All these values are
standard in the literature. The elasticity of substitution between home and foreign non-
commodity goods, θ, is set at 2, which is within the relatively wide range of values
commonly used in the literature. In 2013, the ratio of goods export to GDP in the OECD
national accounts averaged at 20% across the economies in the sample. For 2013, the
Harvard Atlas of Economic Complexity implies an average share of commodities in net
exports for our sample of 85%. Estimates reported in IMF (2012) suggest a lower range of
30–40%, albeit taken over a sample dating back to 1960. We set the share of commodity
exports in total exports at 65%. The share of non-commodity exports in GDP is set at 5%.
With these target values in hand, the implied value for ν, the parameter measuring home-
bias in consumption and investment, is 0.85. We estimate those parameters for which there
is little or no direct empirical evidence: the bond holding cost parameter, ϕb, the
vacancy adjustment cost parameter, ϕv, the investment adjustment cost parameter, ϕx, and
the share of unemployment in the matching function, ζ. Given the choice of the replacement
ratio, the dynamics of unemployment and vacancies depend on the relative consumption share
of the unemployed to the employed agents, cssu/cssw, or equivalently the gap between the
two, Φ = cssw − cssu. Consequently, we allow the data to determine the value of the
consumption ratio.

<hs>  Performance of the model</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~

The red solid lines in Fig. 1 denote the fitted impulse responses of the baseline model.
The corresponding parameter estimates and standard errors are reported in the bottom half
of Table 2. Our model is able to closely replicate the dynamics of the 10-variable PVAR.
For most variables, the model impulse responses capture the shape of the PVAR and lie
within the error bands of its median response. Importantly, the model matches the initial
impact and the approximate paths of unemployment and vacancies. To account for the slight
‘hump-shaped’ path of vacancies, the estimation yields a value for the vacancy adjustment
cost parameter, ϕv, of 0.45. The accompanying standard errors are small. The model is able
to reproduce the initial decline and the following gradual decrease in unemployment,
albeit compared to the data, the path of unemployment is somewhat more persistent. The
model cannot account for the initial decline or indeed the shape of the path of CPI-based
real wages, and the baseline model somewhat underpredicts the volatility of individual
hours. The commodity price rise transmits through a wealth effect to the economy as it
induces a transfer to households. These transfers are used to boost consumption and
domestic investment and to increase savings in the form of foreign bonds. Consumption in
the model rises by around 0.2% and closely tracks the path of consumption in the PVAR. The
theoretical model does rather less well in capturing the dynamics of chain-linked GDP. The
data is far more volatile than the model suggests. Investment in the model closely tracks
both the magnitude as well as the path of investment implied by the PVAR. The investment
adjustment cost parameter, ϕx, takes the value of 0.5. The rise in consumption pushes up
demand for both the domestic and the foreign non-commodity good, although the appreciation
in the real exchange rate holds back demand for the former. In the short-run, the output
expansion is driven by the increase in employment, while over time the gradual buildup of
the capital stock also contributes to the modest rise in production of the domestic non-
commodity good. The shape and the magnitude of the impulse responses depend on the real
interest rate movement induced by the shock under the international financial market
arrangements and on the household's decision on how to allocate the additional transfers
towards savings in foreign bonds, consumption, and investment. In our framework the
interest rate faced by households and firms is equal to the world interest rate adjusted
by a small risk premium that declines with the country's net foreign asset holdings as in
Schmitt-Grohé and Uribe (2003). The elasticity of this risk premium to the net foreign
asset position of the home country, ϕb, is estimated at 0.25 indicating that international
risk sharing is limited.11 In the data as in the model, the rise in domestic consumption
occurs alongside a real exchange rate appreciation which further suggests that country-
specificconsumption-risk from the shock cannot be effectively shared via relative price
movements or trade in bonds. This feature differs from the transmission of a technology
shock in the open economy. Cole and Obstfeld (1991) point out that movements in the terms
of trade provide a powerful source of insurance against technology shocks independently of
the financial market arrangements— with the exceptions of a low trade elasticity of
substitution or permanent technology shocks stressed in Corsetti et al. (2008). An
institutional arrangement that might insulate commodity-producing countries from the
consequences of price fluctuations are sovereign wealth funds. The Norwegian Government
Pension Fund is probably the most widely known example of such a fund. Focusing on the
role of the fiscal policy regime, Pieschacon (2012) argues that the presence of this
sovereign wealth fund helps in insulating the Norwegian economy from commodity-price
related fluctuations.12 Results that we reported in the Appendix to the working paper
version suggest a similar conclusion: after a commodity price increase Norway appears to
run up its net foreign asset position by much more relative to the size of the shock than
the three countries in our sample and thereby it strongly reduces the effect of the shock
on consumption and investment in the near and medium term. Turning to parameters
pertaining to search and matching in the labour market, we find that the share of
unemployment in the matching function, ζ, is highly significant and comes out at 0.758
which is consistent with the literature reviewed in Mortensen and Nagypal (2007). Our
estimates imply that the bargaining weight of households, ξ, assumes the value of 0.3
which suggests that firms have a rather higher weight in the wage bargaining process than
workers. Finally, we find that unemployed members of a household enjoy about 54% of the
consumption of employed agents. With the replacement ratio set at 40% of steady state
wages, there is a modest, but far from complete, requirement to reduce consumption
inequality between household members. We embed the discussion of the role of this
parameter in influencing labour market dynamics and of the plausibility of its estimated
value into the discussion of the transmission mechanism following next.

<hs>  Transmission mechanism</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

The top two panels of Fig. 3 assess the relative importance of the productivity and the
international channels by economic disturbances and time horizon. The top panel shows the
movements of labour market tightness (with positive vacancy adjustment costs as estimated)
in response to a commodity price increase along with the contributions of labour
productivity and the real exchange rate to these movements. Taken together the
productivity and the international channels as approximated by Eq. (12) account for the
bulk of the movements in labour market tightness. As the commodity price increase triggers
an immediate appreciation of the real exchange rate, but only a slow improvement in labour
productivity, the international channel determines labour market tightness in the periods
following directly the realisation of the shock. Following the logic in Bodenstein et al.
(2011), the improvement in the commodity trade balance due to a commodity price increase
must be accompanied by a worsening of the non-commodity trade balance over time as under
rational expectations the absolute value of the net foreign asset position is bounded away
from infinity. This worsening of the non-commodity trade balance is induced by a swift
rise in the relative price of the domestically produced good which in turn translates into
the observed appreciation of the real exchange rate. By contrast, labour productivity
improves little on impact. Although firms are willing to increase investment in light of a
higher marginal product of capital (due to the exchange rate appreciation) and a reduced
real interest rate (due the improved net foreign asset position), the gradual expansion of
the capital stock raises labour productivity only over time. Thus, as the international
channel wanes in importance for the dynamics of labour market tightness, the productivity
channel gains momentum. The ability of our model to deliver data-congruent movements of
labour market tightness in response to a commodity price shock is tightly linked to the
relatively low estimated degree of international risk sharing. Higher degrees of risk
sharing, reduce the real exchange rate response and thus the contribution of the
international channel to movements in labour market tightness. In the extreme case of
setting the bond holding cost parameter ϕb very close to zero, the model converges to a
simple permanent income model with an exogenously fixed real interest rate and barely any
appreciation of the real exchange rate. As result, the response of labour market tightness
is almost nil for this specification of the model. Under financial autarchy, the real
exchange rate movement becomes too amplified and both vacancies and unemployment are too
volatile relative to the data. The transmission of a commodity price shock differs
significantly from the transmission of a technology shock. A positive neutral technology
shock raises labour productivity persistently on impact while inducing a depreciation of
the real exchange rate. The middle panel in Fig. 3 decomposes the response of labour
market tightness after a neutral technology shock into the movements due to labour
productivity and due to the real exchange rate. In this case, the productivity channel
shapes the response of labour market tightness at all horizons. The depreciation of the
real exchange rate is too small for the international channel to play a meaningful role
for the dynamics of labour market tightness under the technology shock.

<hs>  Amplification of shocks and the labour market</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

This interplay between the parameters ru and Φ in amplifying the labour market response is
not unique to the open economy context. Since Shimer (2005) argued that the textbook DMP
model with Nash bargaining and CRRA preferences explains less than 10% of the volatility
in U.S. unemployment and vacancies when fluctuations are driven by productivity shocks,
the “correct value” of the replacement ratio has been the subject of lively discussion.
Hagedorn and Manovskii (2008) and Hall (2008) argue that the flow value of unemployment
ought to capture the value of leisure and home production in addition to the direct
insurance payments to the unemployed. In a final assessment of the search and matching
framework, we construct a prediction for labour market tightness from Eq. (12) using the
estimated impulse responses of labour productivity and the real exchange rate to a
commodity price shock. The bottom panel of Fig. 2 compares this approximation (dashed red
line) to the empirical impulse response of labour market tightness which is depicted by
the solid blue line.15 This approach predicts labour market tightness to respond similarly
to its counterpart in the data after a commodity price shock. Judged by their respective
peaks the magnitudes of the responses are similar, although the timing of the responses is
shifted since the approximation in (12) does not account for time leads and lags.

<h>SENSITIVITY</h>
-----------

Thus far we have abstracted from the use of resources in the extraction of commodities and
the production of non-traded goods. Both these features introduce the possibility for
labour and capital to reallocate into and out of the traded goods sector, the non-
commodity sector in the baseline model.

<hs>  Resource-intensive commodity extraction</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As our discussion of Fig. 2 highlights, the share of employment in the commodity-producing
sector is small for the economies in our sample and the bulk of the pickup in total
employment after an increase in commodity prices occurs in the non-commodity sector. These
findings also point to the existence of frictions in reallocating labour and capital from
the production of goods to the production of commodities. In Fig. 4, the solid lines
depict the impulse responses from an extended PVAR that includes data on employment in the
non-commodity sector and in the commodity-producing sector. The lines labelled Model 2
show the fitted impulse responses of the model in which commodity extraction requires the
use of labour and capital. The extended model is able to capture the empirical dynamics of
employment both in the non-commodity sector as well as in the commodity-producing sector
of the economy. The estimated impulse responses of the remaining variables are roughly
identical to those in Fig. 1 despite differences in the data used to estimate the
underlying PVARs. In response to an increase in commodity prices, employment in both
sectors increases, but given the small relative size of the commodity-producing sector,
most of the variation in employment is driven by the increase in employment in the non-
commodity sector. To properly size the increase in the use of labour in the commodity-
producing sector, the model requires sizeable adjustment costs in labour and capital. In
line with the evidence discussed earlier, the implied expansion in commodity production is
small. Finally, adding employment in the commodity-producing sector has only a minor
effect on the previously estimated model parameters reported in Table 2.

<hs>  Non-traded goods</hs>
  ~~~~~~~~~~~~~~~~

When all domestically produced goods are fully traded, the wealth effect associated with
the commodity price increase must lead to higher demand and production of the domestically
produced traded good for the model to replicate the empirical responses of the labour
market variables. Sufficient home bias in consumption and limited substitutability between
domestic and foreign traded goods guarantee this outcome. When some domestically produced
goods are not tradable, the appreciation of the terms of trade may cause the demand and
production of domestically produced traded goods to decline. If the non-traded goods
sector expands in response to the commodity price increase, the model can still replicate
the empirical responses. Whether the economy experiences this Dutch disease effect
analysed in Corden and Neary (1982) depends on the substitutability between the
domestically produced and the foreign traded goods and the substitutability between traded
and non-traded goods. The dashed lines in Fig. 4, labelled Model 3, shows the fitted
impulse responses of a model with both resource-intensive commodity extraction and a non-
traded goods sector. Overall, Model 3 provides a similar fit to the data as Model 2.
Noteworthy differences in the estimated parameters reported in Table 2 are the smaller
investment adjustment cost parameter (some investment goods are now non-traded, making
investment less volatile) as well as the larger bargaining weight of the households. While
the estimate for the parameter governing the costs of bond holdings is reduced for Model
3, risk sharing is still rather limited. In matching the impulse response functions of the
model with non-traded goods to the data, we set the elasticity of substitution between the
two traded goods at 2 and the elasticity of substitution between traded and non-traded
goods at 0.74 as in Mendoza (1991). For this specification, the economy experiences the
Dutch disease effect after an increase in the commodity price. As shown in Fig. 5
employment in the traded goods sector drops sharply, as does production (not shown). By
contrast, the increase in employment in the non-traded goods sector more than compensates
for this drop, so that, in accordance with the data, total employment expands (with a
small contribution from the commodity-producing sector). In theory, the Dutch disease
effect can be tempered, if not eliminated, by either lowering the elasticity of
substitution between the two traded goods or by raising the elasticity of substitution
between traded and non-traded goods. When commodity prices increase, the price of both
non-traded and domestically produced traded goods goes up— in the case of integrated
factor markets and identical technologies, prices go up by the same amount. Since the
price of the foreign good is determined in the world market and does not change in this
experiment, the terms of trade depreciate and the price of the traded good (an aggregate
of the domestically produced and the foreign trade good) rises by less than the price of
the non-traded good. If the traded and the non-traded goods are sufficiently
substitutable, the demand for both the foreign and the domestically produced traded good
rises (due to home bias and limited substitutability between traded goods). Fig. 5 shows
that employment in the domestic traded goods sector expands when the elasticity of
substitution between traded and non-traded goods is raised to 3 while maintaining the
elasticity of substitution between traded goods at 2. When maintaining the elasticity of
substitution between traded and non-traded goods at 0.74, the demand for both traded goods
can also rise under a low elasticity of substitution between the two traded goods. Fig. 5
shows that employment in the domestic traded goods sector expands when the elasticity of
substitution between traded goods is lowered from 2 down to 0.75. We estimated the model
under alternative parameter choices for the substitution elasticities between goods.
Overall, a good fit of the model to the empirical impulse responses requires the
elasticity of substitution between traded goods to be above unity. Assuming that the
elasticity of substitution between traded and non-traded goods is low (around 0.74), it
appears therefore likely, that the countries in our sample suffer from the Dutch disease
effect after an increase in commodity prices. Absent high quality data on traded and non-
traded goods at quarterly frequency, this prediction of the model is rather strong.

<h>CONCLUSION</h>
----------

Using a structural PVAR and a standard small open economy model augmented by commodity net
exports and search and matching frictions in the labour market, we find: Even advanced
commodity exporting countries are restricted in their ability to smooth out the effects of
commodity price fluctuations through financial markets and relative price movements. To
match the empirical dynamics of the trade balance and the real exchange rate, the
theoretical model requires a low degree of international risk sharing. Matching the
empirical movements in the real exchange rate is also essential to obtain data-congruent
movements in unemployment and vacancies in the model. We show this using a novel
decomposition of labour market tightness into a labour productivity channel and an
international channel that captures movements in the real exchange rate. This
decomposition suggests that the open economy dimension is important in understanding the
transmission of shocks to aggregate demand components to labour market tightness. In
addition to the international channel, the model also requires a preference specification
that drives a wedge between the consumption of the employed and the unemployed household
members for sufficient amplification of the commodity price shock to the labour market.
These findings are robust to augmenting the model with resource-intensive commodity
extraction and non-traded goods. In the presence of non-traded goods, the economy is
highly likely to experience the Dutch disease effect after a commodity price shock.


<h>REFERENCES</h>
----------

  [1] Özge Akinci. Global financial conditions, country spreads and macroeconomic fluctuations in emerging countries. doi:10.1016/j.jinteco.2013.07.005
  [2] David Andolfatto. Business Cycles and Labor-Market Search
  [5] Martin Bodenstein, Christopher J. Erceg, Luca Guerrieri. Oil shocks and external adjustment. doi:10.1016/j.jinteco.2010.10.006
  [8] Harold L. Cole, Maurice Obstfeld. Commodity trade and international risk sharing. How much do financial markets matter?. doi:10.1016/0304-3932(91)90023-H
  [9] W. M. Corden, J. P. Neary. Booming sector and de-industrialisation in a small open economy.. doi:10.2307/2232670
  [10] Giancarlo Corsetti, Luca Dedola, Sylvain Leduc. International risk sharing and the transmission of productivity shocks. doi:10.1111/j.1467-937X.2008.00475.x
  [13] Marcus Hagedorn, Iourii Manovskii. The cyclical behavior of equilibrium unemployment and vacancies revisited. doi:10.1257/aer.98.4.1692
  [17] M. Ayhan Kose. Explaining business cycles in small open economies 'How much do world prices matter?'. doi:10.1016/S0022-1996(01)00120-9
  [19] E. G. Mendoza. The terms of trade, the real exchange rate, and economic fluctuations. doi:10.2307/2527429
  [20] Monika Merz. Search in the labor market and the real business cycle. doi:10.1016/0304-3932(95)01216-8
  [22] Dale T. Mortensen, Éva Nagypál. More on unemployment and vacancy fluctuations. doi:10.1016/j.red.2007.01.004
  [23] Anamaría Pieschacón. The value of fiscal discipline for oil-exporting countries. doi:10.1016/j.jmoneco.2012.03.001
  [24] Christopher A. Pissarides. Short-run equilibrium dynamics of unemployment, vacancies, and real wages
  [25] Morten O. Ravn, Stephanie Schmitt-Grohé, Martín Uribe. Consumption, government spending, and the real exchange rate. doi:10.1016/j.jmoneco.2012.02.001
  [26] Stephanie Schmitt-Grohé, Martín Uribe. Closing small open economy models. doi:10.1016/S0022-1996(02)00056-9
  [27] Stephanie Schmitt-Grohé, Martín Uribe. HOW IMPORTANT ARE TERMS-OF-TRADE SHOCKS?. doi:10.1111/iere.12263
  [28] Robert Shimer. The cyclical behavior of equilibrium unemployment and vacancies. doi:10.1257/0002828053828572
<ART>Competition in the economic crisis: Analysis of procurement auctions
====================================================================

Authors: Klaus Gugler, Michael Weichselbaumer, Christine Zulehner
DOI: 10.1016/j.euroecorev.2014.10.007
Year: 2015  |  Pages: 35-57
ASJC codes: 2002, 2003
Keywords: Construction procurement, Economic crisis, First-price auctions, Government stimulus, Private values

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We study the effects of the recent economic crisis on firms' bidding behavior and markups in sealed bid auctions. Using data from Austrian construction procurements, we estimate bidders' construction costs within a private value auction model. We find that markups of all bids submitted decrease by 1.5 percentage points in the recent economic crisis, markups of winning bids decrease by 3.3 percentage points. We also find that without the government stimulus package this decrease would have been larger. These two pieces of evidence point to pro-cyclical markups.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The recent financial crisis provides a unique testing ground for analyzing causal economic
relations. Although some economists warned of the bubbly nature of asset prices (e.g.
house prices, see Shiller, 2005), the financial crisis and the ensuing economic crisis
were unforeseen.1 We use the current economic crisis to shed light on how markups move in
response to an exogenous shock in demand. We investigate firms׳ competitive behavior in
procurement auctions before and during the crisis; and build a bridge between micro-level
behavior and the effects of macro-level shocks. The recent economic crisis allows testing
for (at least) two effects. First, it enables us to estimate the effects of the recent
economic shock on fundamental structural characteristics of the economy. In particular, we
test for the effects of the shock on the process and intensity of competition, i.e.,
pricing behavior and markups. Second, the effects of fiscal policy can be tested in an
unprecedented manner. In normal times, the effects and determinants of fiscal policy are
difficult to ascertain due to their endogenous nature. Activist fiscal policies in the
crisis are clear cut and mostly targeted to specific industries like the construction
sector. Thus, we can test for the effects of fiscal policy by constructing a proper
counterfactual allowing us identification. We use data from before the economic crisis to
predict what would have happened but for the state stimulus intervention. Our theoretical
reasoning and strategy of identification are as follows. In “normal” times (in the years
before the recent economic crisis) firms operate at their equilibrium capacity utilization
rate. Sometimes they are unconstrained, but sometimes they hit their capacity constraint.
Using data from highway procurement auctions, Jofre-Bonet and Pesendorfer (2003), for
example, estimate that firms are capacity constrained in 32% of the contracts during the
“normal” economic time period 1996–1999, and find that bids are 18% higher if all bidders
are constrained. This implies that economic rents are higher, if firms are capacity
constrained. The negative demand shock resulting from the economic crisis relaxes capacity
constraints: bidders have idle capacity. Given idle capacity, they participate more often
in the remaining auctions and bid more aggressively since their costs are lower. In a
dynamic model, if firms are capacity constrained, they may also price into their bids the
lost option value of winning today versus winning later, i.e. the (additional) cost of
winning today consists also of the loss of future discounted profits due to limited
capacity. Our results are based on an auction model fitted to detailed and comprehensive
data from procurement auctions in the Austrian construction sector in the period 2006 to
2009. Using the start of the downturn as a quasi-experiment, the model enables us to show
how firms react to the massive negative demand shock. The economic crisis has led,
however, governments in many countries to implement stimulus packages and counteract these
negative shocks. This has fueled interest in and discussion of the questions if, how and
which government measures are effective. The Austrian government also implemented a
stimulus package in response to the economic crisis. The main target was the construction
sector. Applying the same logic as above, the government intervention should — ceteris
paribus — increase markups. The focus of stimulus measures on the construction industry is
not idiosyncratic for Austria. Many countries implemented stimulus measures, of which the
construction sector plays a large part. In Austria, the share of the stimulus packages
covered by construction spending was about 22% in 2009. In Germany, about 17% of the
stimulus in 2009 and 2010 were directed to construction. In the US, the share was about
13% in 2009. Thus, we believe that our results are relevant for fiscal policy in general
and are not confined only to Austria. For the empirical implementation, we follow and
simplify Athey et al. (2011) and use a parametric version of Guerre et al. (2000) to
recover the distribution of bidder costs from the observed bids. We assume that the demand
shock exogenously changed bidders׳ participation.2 The distribution of bidders׳ costs is
estimated based on the assumption that in equilibrium the estimates of the distribution
function summarize bidders׳ beliefs and can be used to infer bidders׳ costs based on the
first-order conditions of optimal auctions. Estimation of the distribution of bids is
based on auction characteristics, firm characteristics as well as the level of competition
to which firms are assumed to respond optimally. We utilize a detailed data set that
includes a rich set of variables. Our data set covers nearly the population of all public
procurement auctions in the construction sector in Austria during the years 2006 to 2009.
It includes auction specific variables such as the engineers׳ cost estimates of one firm
for each project and the identities and bids of participating bidders. By matching to a
firm-level database and combining it with data on travel distances from the firm׳s address
to the location of the project, several bidder-specific variables are added. We are thus
able to control for bidder heterogeneity in the econometric model. We show that the crisis
indeed had the expected effects on competition: the negative demand shock led to more
bidders in the remaining auctions and these bid more aggressively. We find a significant
decrease of the average markup in the crisis period of about 1.5 percentage points
relative to a pre-crisis mean markup of 12%. The winning bids are 3.3 percentage points
lower relative to 22.9% pre-crisis. Extending our analysis to the dynamic model of Jofre-
Bonet and Pesendorfer (2003) shows that the main crisis effect is robust to the
incorporation of the option value effect of winning. Markups increase by about 2
percentage points overall in the dynamic model. The crisis drop is about 2 percentage
points for all bids and about 4 percentage points for winning bids. We attribute the
decrease in markups mainly to two characteristics that are affected simultaneously by the
negative demand shock: lower backlogs of firms and an increase in the number of bidders.
Because of the unforeseeable nature of the recent financial crisis, firms did not reduce
their capacities to the lowered demand level. Exit did not immediately follow. Roughly the
same number of firms bid for a reduced number of projects and consequently more firms bid
for each project. More competition and reduced marginal costs lead to lower markups and
lower prices. A counterfactual analysis provides an estimate of the effect of the stimulus
on markups. In this counterfactual, we reduce the backlogs of bidders by the amount the
government spent on stimulus in the construction sector. Our estimate indicates that the
drop in markups would have been about a third higher — increasing from 1.5 to 2 percentage
points — without government stimulus. While the macroeconomic literature compares markups
over the business cycle across industries,3 we follow the microeconomic literature and
estimate bidders׳ cost distribution from submitted bids in construction procurement
auctions.4 By focusing on one industry and imposing the structure of a game-theoretic
model we are able to back out firm specific cost and do not have to rely on data averaged
over firms. We have to assume, however, that bidders behave according to the theoretical
model.5 In the literature, construction procurement auctions have been extensively
studied. Jofre-Bonet and Pesendorfer (2003) show non-parametric identification in repeated
auction games and using a parametric model for the estimations, they find evidence of
capacity constraints in Californian highway procurement auctions. Krasnokutskaya (2011)
proposes a nonparametric estimation method to recover the distribution of bidders׳ private
information when unobserved auction heterogeneity is present and finds that private
information is estimated to account for 24% of the variation in bidders׳ costs in Michigan
highway procurement auctions. Balat (2012) looks at road construction in California and
investigates the effect of the American Recovery and Reinvestment Act on equilibrium
prices paid by the U.S. government. He extends the models by Jofre-Bonet and Pesendorfer
(2003) and Krasnokutskaya (2011) and allows for unobserved project heterogeneity and
endogenous participation. His results show that prices rather than quantities increase as
a consequence of the implemented stimulus. Groeger (2014) studies participation and
bidding decisions in repeated highway procurement auctions and the estimated parameters
suggest that participation synergies exist. Further studies accounting for endogenous
participation are Krasnokutskaya and Seim (2011) and Athey et al. (2011, 2013). The
organization of the paper is as follows. In the next section, we describe the construction
sector in Austria and provide insights into the organization of procurement auctions.
Section 3 presents the theoretical background and the econometric model of the
distribution of bidders׳ construction costs. We provide a discussion of the specific
timing of the crisis as it hit the Austrian construction sector and describe the likely
consequences of the crisis on competition. The section also contains details on the data
as well as summary statistics. Section 4 presents and discusses the estimation results.
Based on the estimates, we discuss the effects of the recent economic crisis and the
associated fiscal stimulus on firms׳ costs and markups. In addition, we report robustness
checks as well as counterfactual effects of the model, together with more detailed results
of markups in the stimulus and non-stimulus sector and for specific stimulus projects. The
relation to other findings and competing models as well as possible policy conclusions are
discussed in Section 5. In Section 6, we conclude.

<h>INSTITUTIONAL BACKGROUND</h>
------------------------

This section provides information on Austria׳s construction sector and how the Austrian
government implemented the stimulus packages to combat the economic crisis following the
breakdown of Lehman Brothers. A main part of the stimulus package concerned the
construction sector and thus affected procurement auctions. Finally, we describe the
organizational background of these auctions.

<hs>  Construction sector and stimulus packages in Austria</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In Austria, the construction sector accounts for 7% of GDP on average between 2006 and
2009 (in Germany this share is 4.2%, in the USA 4.4%; OECD STAN data set). As can be seen
from Fig. 1, total construction value added steadily increased from around 10 billion
euros in 1999 to 2002 to 16.2 billion euros in 2008 in Austria in nominal terms. In 2009,
when nearly all countries went into recession due to the financial crisis, total
construction value added fell to 15.5 billion euros, which is a drop of 5% in real terms
(the inflation rate was 0.5%) compared to a drop in real GDP of 3.8%. Building
(corresponding to 2-digit-SIC code 15) and heavy construction (SIC-2: 16) are the two main
subsectors. While building construction remained nearly flat in real terms, heavy
construction value added fell by around 10% in real terms. Like other countries, the
Austrian government responded to the global economic crisis and did this with similar
measures and at similar dates. In October 2008, the Financial Market Stability Act and the
Interbank Market Support Act became effective to support the interbank market, allow the
government to grant guarantees, assume bank liabilities and acquire bank equity. Also in
October 2008, the parliament voted for the first of two stimulus packages. In December
2008, the council of ministers voted for the second stimulus package. The major parts of
the stimulus packages consisted of credit and financing for private companies, a bonus
depreciation plan, additional funds for R&D, subsidies for thermal rehabilitation of
buildings, a car scrappage program (“cash-for-clunkers”) and increased public expenditures
on infrastructure. These infrastructure expenditures were made by advancing investment on
public infrastructure, originally scheduled for years later than 2009 and 2010. In 2009 —
the year when our data end and the first year of stimulus — the stimulus directed at the
construction sector consisted of 363.3 million euros. It was invested into roads, railways
and (public) buildings. Within these categories, it was spread over all sorts of
construction projects: maintenance, rehabilitation, rebuilding and new building of railway
stations, roads, schools, universities, judicial buildings and so on.

<hs>  Organization of procurement auctions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Austria׳s public authorities (federal and regional government, social security
institutions, and the like) are subject to the Federal Public Procurement Law (PPL,
“Bundesvergabegesetz”). Private companies have to follow these rules only if (1) they are
active in a “sectorial activity” (provision of water, mail services, energy, or traffic),
and (2) their activity is regulated (e.g. entry regulations). In principle, there are no
lower limits for the applicability of the PPL. Upper limits are in effect, but only to
enforce EU-wide announcement rules for larger projects (in construction, currently 4.845
million euros). The main purpose of the PPL is to stimulate competition and safeguard
equal treatment of all potential bidders. The law stipulates some restrictions on bidders,
but they do not, in our judgment, affect competition, but are intended to forestall
opportunistic behavior (e.g. the requirement of a 5% bid bond). Except for very small
projects the public authority must choose between an “open procedure” or a “restricted
procedure with publication of a contract notice”. Such projects have to be made public and
documents must be freely accessible. In our sample, 85% of the auctions are “open”, and
only 2% are of the “restricted” type. The remaining 13% were not publicly announced.
Instead, selected qualified companies were invited to submit bids. All contracts are
awarded by first-price sealed-bid auctions. There is no explicit reserve price – the
seller has the right to withdraw the auction when the winning bid is “contra bonos mores”
(offending against good morals). In court, the seller would proof this by providing a cost
estimate that is based on standard commercial and professional principles and has to show
that the winning bid is far higher than this estimate. Each project is described in a
procurement catalogue. The seller defines the components and quantities needed for the
construction project. The bidder provides a unit price for each component. The final price
in the auction is then the sum of prices for the various components multiplied with the
quantity. Bidders who want to participate in an auction have to proof their commercial and
professional abilities before being admitted to the bidding process. On the letting day,
all bids are unsealed, ranked, and the low bidder wins the auction. After the lowest bid
has been identified all bidders are informed. If no bidder objects the decision within 10
days, it is final.

<h>BIDDERS׳ BEHAVIOR BEFORE AND IN THE CRISIS</h>
------------------------------------------

This section describes the theoretical model, the econometric model of the distribution of
bidders׳ construction costs and the hypotheses for our empirical analysis. We also
describe our data and give summary statistics. Our theoretical reasoning and strategy of
identification are based on the assumption that in “normal” times, i.e., in the years
before the Great Recession, firms operate at their equilibrium capacity utilization rate.
Once firms hit their capacity constraints, their costs increase. We then expect economic
rents to be higher. The negative demand shock due to the economic crisis implies that the
capacity constraints are relaxed: bidders have idle capacity in the crisis. Given idle
capacity they participate more often in the remaining auctions and bid more aggressively
since their costs are lower. To estimate the distribution of bidders׳ costs, we implement
a static first-price auction with an exogenously given number of bidders as our main
specification. As robustness checks, we also implement a dynamic first-price auction that
accounts for the strategic effect of capacity constraints following Jofre-Bonet and
Pesendorfer (2003), and a model with endogenous entry following Athey et al. (2011).6 As
our main econometric model is however based on the static model, we stick to the static
theoretical model in the following and provide the respective implementations of the other
models in Appendix A.

<hs>  Estimation of bidders׳ costs</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

To illustrate the econometric model and the structural estimation of the distribution of
bidders׳ construction costs, we use sealed-bid data to estimate the parameters of the
theoretical model as a function of auction and bidder characteristics making use of the
approach developed by Guerre et al. (2000). They suggest to estimate the distribution of
bids in a first step and to recover the distribution of bidders׳ costs in a second step by
using the first order-condition for optimal bidding behavior. With the estimates of the
distribution of bidders׳ costs at hand, we then calculate markups.

<hs>  Timing of the crisis and empirical hypotheses</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In our empirical analysis we want to exploit the economic crisis as a quasi-natural
experiment after which firms in the construction sector start going into public
procurement auctions more often. It is not obvious when the demand changes were perceived
as signs of an economic crisis and consequently when firms changed their behavior.
Nevertheless, we want to identify a rough date when to expect changes borne by the factors
outlined above. Fig. 2 puts developments in the construction sector in a longer time
perspective. Total construction (private and public contracts) displays an upward trend
both in the stock of contracts and new orders — new orders are the gross inflow of new
contracts that are accepted by firms in a given month — up to about 2007. Stocks of
contracts reach a plateau a few months earlier than new orders. Not before September 2009
do the stock values fall short of the level seen in January 2008. Subtracting eleven
months leads to the first possible impact of the trailing moving average. October 2008
then is a potential date when we could expect changes in the bidding behavior of firms if
stock values of contracts are relevant for the bidders. New orders provide early
information on the output of the construction sector in the months that follow.
Construction firms can anticipate their backlog in the near future and may adjust bidding
behavior. A relatively consistent downward movement of new orders starts in March 2009,
which, after subtracting eleven months, gives April 2008 as a second relevant date. In the
crisis demand shrinks, capacity constraints are relaxed, and (roughly) the same number of
bidders bid in fewer auctions, implying an increase in the number of bidders per auction.
Thus, due to this competition effect, bidders bid more closely to their true costs in the
crisis. Fig. 3 shows a striking negative relationship between the number of bidders per
auction and the new orders series in the construction sector (both public and private
contracts).19 While new orders in the construction sector sharply decrease due to the
crisis, the number of bidders per auction sharply increases. New orders in public
procurement (also in Fig. 3), however, are larger in the last few months of 2009.
Accordingly, our backlog measure — after dropping sharply in 2008 — begins to rise again
in early 2009.20 We attribute this to the growing inflow of stimulus projects. To provide
further evidence for our argumentation that the crisis affected the number of bidders in
public procurement auctions and bidders׳ capacity utilization measured by their backlog,
we show descriptive regressions in Table 2. We regress each variable on a dummy variable
that is zero before and one in the crisis — starting in October 2008 — and a time trend to
control for general movements in the time series. The results depicted in Panel A of Table
2 confirm our impressions from Fig. 3. We observe that the number of bidders in an auction
increases in reaction to the crisis. This effect is significantly different from zero and
about one and a third bidder on average. In columns (2)–(5), we present the robustness of
our estimate to placebo treatments. One might be concerned that the increase in the number
of bidders picks up some additional unspecified effects over time. Similar to Black et al.
(2008), we introduce a placebo treatment and add hypothetical crisis dates to the
specification. We use four additional dates for the crisis: two months and six months
before and in the crisis. The estimated coefficient for the change in the number of
bidders does not change significantly. We repeat this exercise for the backlog. We find
that the estimated effect of the crisis on the backlog is negative as expected and
significantly different from zero. Again we run placebo experiments and find that the
estimated coefficient does not vary much over the specifications shown in columns (2)–(5)
in Panel B of Table 2. In the presence of a negative demand shock, the incentive to shade
bids above one׳s cost decreases. A bid is equal to the expected cost of the competitors
conditional on the competitors׳ costs being less than the bid. If there is more
competition in the sense that there are more actual and capacity unconstrained bidders in
an auction, the markup goes down, (1) since the expected conditional cost of competitors
decreases, so bids are closer to costs, and (2) capacity unconstrained bidders bid more
aggressively since their costs are lower. This implies that bidders׳ expected rents go
down in equilibrium and gives the first hypothesis. Hypothesis 1: The markup goes down in
an economic crisis. As argued, our structural approach allows us to measure the impact of
activist fiscal policy. The state intervened drastically during the crisis with the two
stimulus packages, and particularly so in the construction sector. Economically, targeted
fiscal stimulus shifts the demand curve in the construction sector at least partially back
to where it would have been without the crisis. This gives our second hypothesis.
Hypothesis 2: The markup would have decreased by more had the state not intervened in the
construction sector. If validated, both hypotheses imply pro-cyclical markups. The main
underlying assumption of our two hypotheses is that an increase in the number of bidders
yields lower procurement prices and lower bidder revenues. This is a standard competition
argument, but need not always be true. In a model with common values,21 informational
asymmetries such as the “winners׳ curse” may offset the above argument. We argue that the
independent private value model is valid in our context. As described in Section 2.2,
construction projects consist not only of one (final) price, but are actually the sum of
prices for various components expressed in fixed quantities that are known from the
procurement catalogue. Firms put in the prices they are willing to offer for the various
components. As the components of the project are fixed,22 firms then differ only by their
private cost. However, even in an independent private values model as we apply here,
bidder asymmetries23 or costly bidding24 may also lead to the effect that more bidders
could lead to reduced price competition. In our case, the empirical model allows for
bidder asymmetries as we control for firm specific variables such as the distance between
firm location and construction site as well as firm size, and estimate bidder specific
distributions. In addition, we run a robustness check modelling participation. Finally, we
do not consider bidders to be risk averse, but risk neutral. If, however, bidders׳
attitude towards risk would change in the crisis, we may attribute some of the change in
markups incorrectly to competition as risk aversion induces more aggressive bidding than
risk neutrality (Maskin and Riley, 1984).25 While estimating a model with risk aversion
would go beyond this paper, we can at least partially account for changes in risk aversion
over time by splitting the sample and estimating two different cost functions as we do as
one of our robustness checks.26

<hs>  Data and summary statistics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~

One large Austrian industrial construction company provided our main data, containing
bids, firm names and auction characteristics. This data set covers all auctions in both
building and heavy construction in the period January 2006–December 2009, where this
company took part either as the parent company itself or as one of its subsidiaries.
According to the company, the database covers more than 80% of all auctions which must be
conducted according to the Public Procurement Law. Thus our sample covers nearly the
population of all public procurement auctions in Austria during the four years 2006–2009.
Within this period, our database reflects on average 14% of Austria׳s total construction
sector. In 2009, this share is at 16%, which mirrors the increased activity of the state
through the stimulus. This increase is more visible in heavy construction, where our data
set represents 26% of total heavy construction in 2009, up from an average of 21%. Our
data set covers a relatively stable share of 10% of building construction. Of these firms,
1342 or 81%, were matched to Amadeus. Thus, 96% of the total 29,850 bids come from matched
firms. The population of Austrian construction firms, as reported by the Austrian federal
agency, Statistics Austria, consists of 4796 firms on average for 2006–2009 (building:
3958, heavy: 838). Therefore, about one-third of all construction firms submitted bids in
the procurement auctions. Table 4 gives detailed yearly summary statistics on firms,
auctions, bids and competitive structure. Bidder characteristics: We cover many relatively
small firms with an average of around 150 employees (median: 54 employees) and 20 million
euros in total assets (median: 4 million). Auction characteristics: Splitting the sample
into the two main construction sectors reveals that two-thirds belong to building and the
rest to heavy construction. On average, the technical estimate for the projects׳ cost is
2.4 million euros (at 2006 constant prices) and the average winning bid is 4% below that.
Transportation costs play an important role in the construction sector. We measure these
costs by the distance of a firm to a construction site. Based on the construction sites׳
and bidders׳ postal codes, we used Microsoft׳s Bing Maps to calculate the driving
distances for all bidders to the project sites corresponding to the auctions. Postal codes
for virtually all bids are available in our main data. 4-digit postal codes give very
detailed information on location in Austria and exact street addresses can be neglected
without loss of relevant information for our purpose.29 Besides driving distance, we have
also retrieved travel times. While in singular cases the two may differ substantially, the
correlation is very high at 0.973 in our sample. Not surprisingly, all calculations are
robust to the choice between them or the inclusion of both. Mean distances equal 123 km in
2006 and 2007, reach its highest value of 139 km in 2008 and fall slightly to 135 in 2009.
Thus, firms are willing to bid in projects farer away and thus to drive longer distances
to the project sites in the crisis.30 Capacities: Backlog used by a firm at a point in
time is calculated as in Jofre-Bonet and Pesendorfer (2003). Every project is added to the
backlog when a firm wins it. Projects are linearly worked off over their construction
period, which releases capacity. Every firm׳s backlog obtained is standardized by
subtracting its mean and dividing by its standard deviation. We have also experimented
with alternative definitions of backlog but they do not change our findings substantively.
The variable captures all auctions of the company providing us with the data but does not
carry information on backlogs of auctions where this firm did not participate. Although
this company participates in most auctions, potential bias could be introduced. To relieve
the variable from potential bias, additional data about projects won in the past come from
the “Austrian Register of Tenderers”. The register gathers all public procurement tender
offers and information about the winners and often the contract value of past concluded
contracts. We selected those projects where at least one recorded subclassification
belongs to the construction sector (Common Procurement Vocabulary 2-digit code equal to
45). By matching the winning bidder and thus the winning bid, where available, to the main
data set, unbiased procurement backlog data are available for all companies. A backlog
variable needs some precursory data to account for projects already in the books of the
firms when our main data set starts. The additional information from these external data
contains projects before 2006. We go back until 2005, one year before our estimation
sample starts, in our matching. Of the 5235 winning bids in the Register, 42% come from
firms that also bid in our main data. These winning bids correspond to 72.3% of all
project values won in the Register. Keeping in mind that some of the projects from the
Register that we retrieved are primarily other-than-construction projects and have often
only one subclassification from the construction sector, this high percentage of
procurement values from matched firms gives further indication that our main data is
representative. To proxy firms׳ outside option, we use the inflow of new orders into the
construction sector, i.e., a macro variable, in our regressions. Herewith, we can account
— at least to some extent — for contracts that have not been procured. Stimulus sector and
stimulus projects: Stimulus in the construction sector took place predominantly in three
incorporated but government owned institutions for managing public buildings
(Bundesimmobiliengesellschaft), public highways (Autobahnen- und Schnellstrassen-
Finanzierungs-Aktiengesellschaft) and public railways (Österreichische Bundesbahnen). From
public information we could identify which specific projects in the sample were designated
by the government for the stimulus package. 17 of the 561 projects in the estimation
sample in 2009 are part of the stimulus package, representing 3.8% of the total project
value of 2009. These specific projects were scheduled after the year 2009 originally, but
were actively brought forward by the government to counteract the crisis. We thus
differentiate between two types of stimulus by the government. First, the government did
not abandon projects as the private sector did. We call this sector “stimulus sector”, and
it includes essentially the projects of the aforementioned three institutions (and it
includes also the 17 specific stimulus projects). Second, we separately look at these 17
additional projects and call them “stimulus projects”. Relation between engineer estimate
and bids ranked first and second: Table 5 shows the absolute values of the engineer
estimate and the winning bid in columns (1) and (2), tabulated by the number of bidders.
As the number of bidders increases, the relative difference between winning bid and
engineer estimate falls (column (3)). Column (4) reports the number of auctions for each
number of bids submitted in the estimation sample. In the lower part of Table 5, “money
left on the table”, the relative difference of second-ranked to winning bid, which is a
measure of informational asymmetries, is tabulated against the number of bidders. This
relative difference is on average 7.7% and it narrows as the number of bidders increases.
These statistics are consistent with the findings of Jofre-Bonet and Pesendorfer (2003),
Balat (2012) and Krasnokutskaya (2011). Columns (6)–(8) divide the auctions into projects
not in the stimulus sector, in the stimulus sector and the 17 specific stimulus projects
we could identify. “Money left on the table” appears to be larger for stimulus related
projects.

<h>EFFECT OF THE CRISIS ON FIRMS׳ MARKUPS</h>
--------------------------------------

In this section, we describe the estimation results. Based on these results, we calculate
bidders׳ markups. We exploit the recent economic crisis as a quasi-experiment and test
whether firms׳ pricing power is affected by the recent economic crisis and the stimulus.
We then check the results for robustness. Finally, we run a counterfactual analysis to
validate the results from the quasi-experiment and test our empirical hypotheses.

<hs>  Estimation results</hs>
  ~~~~~~~~~~~~~~~~~~

Columns (1) and (2) of Table 6 show the estimates for the scale parameter λ, columns (3)
and (4) for the shape parameter ρ. Backlog (i.e. own backlog) and backlog sum (i.e. the
backlog of the other actual bidders) measures capacity constraints. As expected, both
backlog measures display positive coefficients. Firms bid higher if their own backlog is
higher since they have higher opportunity costs; and firms strategically bid higher when
they know that their competitors have higher backlogs, and therefore higher costs. The
effect of the log of the number of bids is negative — consistent with the notion that more
bidders increase competitive intensity. Note that the log is used to account for the
diminishing influence of an additional bid as the number of bidders grows. The engineer
estimate is the most important determinant of the bid. The log of the number of employees,
our firm specific size measure, has a positive influence on the bid level. KM measures the
driving distance between firm and project site in kilometers. While insignificant, two
other variables derived from the distance data are significant: KM sum, defined as the sum
of competitors׳ distances, and KM average, the average distance of the bidders in the
auction. We interpret these as strategic variables in a limit pricing context: the further
competitors are away from the project site, the higher their costs. When competitors are
further away, a firm can submit higher bids. Besides that, some control variables are
included: same postal code of firm and project site, same district and same state, open
format auctions, heavy construction auctions, and bidder is a general contractor. Fig. 4
compares the kernel densities of actual to predicted bids. The prediction matches the
actual density closely. To assess our two main effects more closely, we show the effect of
the backlog and the number of firms on bids in Fig. 5. For the illustration we chose the
median project. The ranges of backlog and the number of bidders are chosen such that 99%
of all bids are covered. Both variables have the expected sign in the estimation of the
scale parameter. In general, the shape parameter also influences the expected value and
the total effect of a variable in the Weibull distribution is not obvious from the
estimates. For our results, the partial effect of backlog or number of bidders turns out
as hypothesized, too: more bidders in the auction decrease the bid, a higher backlog
increases the bid.

<hs>  Quasi-experiment</hs>
  ~~~~~~~~~~~~~~~~

From our structural estimates we proceed with the calculation of the markup for each
bid.31 With the calculated markups, we test the first hypothesis on the effects of the
economic crisis on markups, i.e., that markups go down in an economic crisis. To obtain
our results, we are interested in the mean difference of markups between before the crisis
started and afterwards. As has been shown in Fig. 2, new orders and stock of contracts
start downward developments in April 2008 and October 2008. If we split the sample in
April 2008, the difference between before April 2008 and after April 2008 in mean markups
is −0.6 percentage points; if we split the sample in October 2008, the difference reaches
significant −1.5 percentage points. The shaded area in Fig. 6 displays these differences
on the black line at the left border of the shaded area (April 2008) and right border of
the shaded area (October 2008). We further show those values when we split the sample at
any arbitrary point in time between April 2006 and October 2009. Note that the sample size
is constant at n=14,845, but the subsample of the first part — the pre-crisis period —
shrinks when we move the crisis start date to earlier months and the subsample of the
second part — the crisis period — grows accordingly. The black line gives the difference
of mean markups before and after a specific month. The dotted lines above and below the
black line show the upper and lower limit of the 95% confidence interval and indicate
whether the difference is significant. Reassuringly, the graph of markup differences
displays a downward trend indicating that the crisis truly reduced markups. The actual
prices paid are determined by the winning bids. Fig. 7 shows the mean markup differences
when only winning bids remain in the calculations. The point estimate of the mean
difference between before April 2008 and after April 2008 is −0.9 percentage points and
therefore larger than for all bids at the same date, but not significant. The difference
becomes −3.3 percentage points if October 2008 is chosen as the crisis starting date, and
this number is both economically large and statistically significant. For the (eventually
relevant) winning bids, therefore, the reduction of markups due to the crisis is more
pronounced. Stimulus sector and stimulus projects: In Table 7, we distinguish between all
projects, projects in the stimulus sector and stimulus projects. Distinguishing the
markups for these subgroups is of descriptive interest. We observe that markups in the
stimulus sector are higher than average markups. This is true before and in the crisis. We
also observe that the drop in markups is more pronounced in the stimulus sector than on
average. Markups of stimulus projects are larger than markups in the stimulus sector, when
we consider all bids. Summarizing, from our structural estimates we conclude that markups
decrease in the economic crisis and confirm Hypothesis 1.

<hs>  Threats to identification</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~

The identification of our results strongly depends on the assumption that the crisis is a
quasi-experiment that exogenously decreased the demand for construction projects. We argue
that there was a sudden downturn in the construction sector caused by the crisis and
essentially the same number of firms is competing for fewer projects. As a consequence we
observe a higher number of bidders per project, more competition in the procurement
auctions and, therefore, lower equilibrium prices and lower markups. The advantage of our
empirical setup is the clear time-line and its simplicity. The crisis is an exogenous
demand shock, and we restrict our attention to a simple static framework. There are,
though, threats to our identification. One could think that not only demand was affected,
but also bidders׳ cost. In the crisis, credit access and interest rates as well as input
prices may have changed. One other source of concern might be the effect of the engineer
estimate. Since one firm provided us with the data, it could be biased towards any
idiosyncrasy of that firm and yield biased estimates of bidders׳ costs. It is also
conceivable that the largest firms behave differently than the fringe firms. In addition,
we do not account for unobserved auction specific heterogeneity and endogenous entry.
Finally, as we do not consider the dynamic strategic effect of backlogs, we may
misinterpret our results due to an omitted variable bias. In order to confront these
problems we provide additional pieces of evidence that should lend credibility to the
interpretation of our results as market responses to the exogenous demand shock. First, we
investigate whether bidders׳ cost distributions have changed in the crisis. We split the
sample into the period before and during the crisis and estimate bidders׳ cost
distributions separately for these two periods. Second, we address the engineer estimate
and look at several modifications of our sample. Third, we include fixed effects for the
seven largest firms.32 Fourth, we allow for unobserved heterogeneity, endogenous entry or
dynamic considerations. When we model bidders׳ costs, we assume that the set of auction
characteristics is known to the econometrician and to the bidders. To relax this
assumption, we follow Krasnokutskaya (2011) and allow for unobserved heterogeneity.
Neglecting entry cost or the dynamic strategic effect may bias our results. Thus, we
estimate a model with endogenous entry similarly to Athey et al. (2011) and a dynamic
model following Jofre-Bonet and Pesendorfer (2003).33 Our first robustness check allows
the cost distribution to differ across periods. Panel A of Table 8 presents the estimated
coefficients of the cost distribution before the crisis and Panel B during the crisis. We
observe that, for example, the estimated coefficients for the number of bidders and for
the backlog differ. The effect of the number of bidders becomes stronger in the crisis,
whereas the effect of the backlog becomes weaker. This reinforces our main argument how
the crisis affected this market: competition increases and capacity constraints relax. We
then calculate the markups based on these cost distributions and present them in Table 9.
Column 1 contains the results from the base model for comparison. The second column, R1,
shows the estimated markups when we allow the cost distribution to differ over the two
periods. Our main result of lower markups in the crisis holds. Interestingly, the
difference is slightly more pronounced on average. This is true for all bids and for the
winning bids. The next three robustness checks in Table 9 address the engineer estimate in
one way or the other.34 For column R2, the bids of the firm supplying the engineer
estimate are omitted from the estimation of the determinants of bids. Results are robust
to this modification. In R3, the engineer estimate variable is dropped altogether, nearly
doubling the sample size. Although the crisis drop in markups is still present, the
magnitude of markups is much larger than in the base estimate. Clearly, one has to control
for auction size. For the next check, R4, also auctions with very poor engineer estimates,
in terms of large deviations from the bids that were submitted eventually, were included.
Consequently, the sample size is a bit larger than that of the main results in Table 6.
While average markups increase, the pre-crisis–crisis pattern remains. R5 shows the
results when fixed effects for the largest seven firms in terms of total number of bids
submitted in the sample are included. The fixed effects permit a somewhat different
behavior by the largest firms, similar to the split into main bidders and fringe firms
found in Jofre-Bonet and Pesendorfer (2003) or Athey et al. (2011). Results are robust to
the inclusion of firm fixed effects.35 In the next column, R6, the model switches to a
Weibull-Gamma-mixture distribution to permit unobserved auction heterogeneity similar to
Krasnokutskaya and Seim (2011) and also Athey et al. (2011). Average markups go down, but
again our main result of decreased markups in the crisis holds up. In column R7, we
account for entry. The results are very close to the markups calculated in the base model.
Winning bids׳ markups are slightly larger after accounting for entry. Looking at the
markup difference pre-crisis versus crisis, both sets of simulated markups yield results
close to the base model. In column R8, we depict the results from the dynamic model.
Again, our main result prevails, although — as expected — estimated markups are higher
when we account for the dynamic strategic effect. Overall, our results are robust to a
number of modifications of our main specification.

<hs>  Counterfactual analysis</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

Three counterfactual experiments help to validate the results: two for the quasi-
experiment and one to give a quantitative measure for our second hypothesis, i.e., the
markup would have decreased by more had the state not intervened in the construction
sector. To model the crisis, we manipulate the number of bidders and the backlog (own
backlog, other bidders׳ backlog and new contracts). We conduct the analysis for the base
model and the dynamic model. The split date for the pre-crisis vs. crisis period is the
start of October 2008. For each experiment, we recalculate the bids and the backed out
cost valuations. Bids are predicted using the Weibull model (5) from the base
specification. To obtain predictions for bidders׳ cost, we estimate a Weibull model using
as covariates variables that influence a bidder׳s cost such as own backlog, new contracts,
distance, number of employees and the engineer estimate.36 For the counterfactual
analysis, we manipulate own backlog, backlog of others, new contracts and the number of
bidders in the bid distribution and own backlog and new contracts in the cost
distribution. In the first experiment, we address the following question: what are the
markups if the competitive situation did not change in the crisis? We apply the pre-crisis
competitive environment in terms of number of bidders and bidders׳ backlogs to projects in
the crisis. We define this environment as one bidder less and a backlog that is increased
by one standard deviation. We also increase the value of new contracts by 5% to account
for bidders׳ outside option in the private sector. According to the model, fewer bidders
and higher backlogs will then lead to higher markups. Table 10 shows the implications of
the base model and the dynamic model for all bids and for the winning bids. For both, all
bids and winning bids, we first show the mean markups for the base model and then for the
dynamic model. The results from our first experiment show that we can replicate our quasi-
experimental results very well on average. Depicted in column (1), we predict average
markups of 12.53% for projects procured in the crisis but evaluated in a pre-crisis
environment (+1bl., −1n.). This value is close to the actual markup of 12.04%.
Qualitatively we do not observe differences between the static and the dynamic model.
Markups estimated from the dynamic model are on average by about two percentage points
higher than markups estimated from the static model. Again, the experiment shows that we
can replicate our quasi-experimental results very well on average. Evaluating projects
procured in the crisis in a pre-crisis environment (+1bl., −1n.), we predict average
markups of 14.00% close to the actual markup of 13.96% depicted in column (3). Projects
before and during the crisis are not identical. The second experiment uses the pre-crisis
projects and fixes the auction characteristics to answer the question: what happens to
markups if the increased competition and lower backlog levels in the crisis would have
been present before the crisis? We herewith control for changes in the composition of
projects. We turn around the counterfactual from the previous experiment and apply it to
pre-crisis projects (“−1bl., +1n.”). Given one additional bidder and lower capacity
utilization before the crisis on the very same projects before the crisis leads to
counterfactual effects that support the evidence from the first counterfactual. Thus, our
results are robust to a change in the type of projects in the crisis. To model the
government stimulus, we reduce the backlog of those bidders that won projects in the
stimulus sector in the crisis. The question here is as follows: what is the quantitative
effect of the government stimulus? We take the 17 stimulus projects that we were able to
identify through parliament reports. We then randomly draw further projects in 2009 to
reduce the backlog by the amount of the government stimulus directed to the construction
sector, totalling 363.3 million Euro. The number of bidders increases by another one-third
of a bidder relative to the crisis environment and the value of new contracts decreases by
2.5%. In this way, we aim to quantify the effects on bidding were there no government
intervention. Lower backlogs and more bidders will lead to lower markups. To account for
the fact that the government stimulus was implemented in the crisis, we apply the
experiment to the crisis observations. The results of the counterfactual analysis support
our second hypothesis. If the government had not intervened, markups would have dropped by
more than we observe. Our third experiment provides the evidence. Using the estimates from
the static model, we observe a counterfactual markup of 10.02% for all projects, on
average. Compared to the observed markup of 10.52%, this is an additional drop of half a
percentage point. This drop is slightly larger when we consider the estimates from the
dynamic model. This difference may illustrate the lost option of winning tomorrow. Markups
in columns (2) and (4) of Table 10 are for winning bids. While the markups are much higher
for the winning bids, the general pattern, i.e. drop of the markup in the crisis, partial
reversion of the drop in the markup due to the stimulus, is similar. The counterfactual
analysis confirms the results we obtained for all bids, although the predictions for
winning bids are less precise. Our results are robust to the specification of the model
and we can also confirm our second hypothesis. As in the pre–post quasi-experimental
analysis, we also observe in our counterfactual analysis that markups are pro-cyclical.
The additional demand due to the stimulus package increased markups. Moreover, possible
crisis-related changes in the type of projects do not drive our results.

<h>DISCUSSION</h>
----------

Comparisons of pre-crisis and crisis markups consistently confirm Hypothesis 1: in the
crisis, markups drop. Pre-crisis projects in the stimulus sector in general and the 17
stimulus projects in particular exhibit higher markups, but fall almost to the lower
crisis markup level of projects not in the stimulus sector. It seems that the change in
the competitive environment levels markups over different types of projects. We also
provide evidence for Hypothesis 2, which says that the fiscal stimulus weakened the crisis
drop in markups. Absent the stimulus, our counterfactual analysis shows that backlogs
would have dropped further and (even) lower demand would have increased the number of
bidders by more in the remaining auctions. Markups would have decreased by more, given the
influence of backlog and number of bidders in the model. Thus, the two pieces of evidence
consistently point to pro-cyclical markups. While developing a new method to analyse a
structural dynamic auction with unobserved heterogeneity and endogenous entry, Balat
(2012) looks at a specialized construction subsector, namely road construction. These
specialized construction firms do not face demand reduction from the private sector,
because demand comes from the state. As the state increases spending on road construction
as part of the stimulus, these firms actually experience increased demand. From the
perspective of the economy-wide construction sector this is a special situation, because
overall demand is reduced in the crisis, as we have shown. Balat (2012) finds that markups
increase in the situation of demand increase, analogously to the markups decrease we find
when demand decreases for the whole construction sector. Our results show that the pro-
cyclicality of the markup is witnessed in both situations — increases and decreases of
demand. Our results also show that the increased prices of government projects in Balat׳s
(2012) study carry over to the other, more general construction sectors in our
environment. The typical motive for government spending in a recession is stimulation of
the economy. We find that the government also faces lower markups and therefore lower
prices for its projects. Domowitz et al. (1986) give empirical evidence on business cycles
and their influence on the relationship between concentration and (average) price-cost-
margins. They observe pro-cyclical margins in concentrated industries. As explanations,
models of collusion and models of cost differences are suggested.37 With their industry-
level data they do not give evidence allowing to discriminate between the explanations.
Other recent studies by Nekarda and Ramey (2010, 2011) are also interested in testing the
effects of government stimulus on markups — in particular in the context of different
predictions from neo-classical and neo-Keynesian business cycle models. From neo-Keynesian
models they expect countercyclical markups, given that prices are sticky while wages would
increase due to demand increases, and therefore marginal cost would increase. The authors
find pro-cyclical markups as we do, however, neither with economy-level nor with industry-
level data do they find an effect of government stimulus on markups.

<h>CONCLUSIONS</h>
-----------

We estimate the cost distributions of construction firms based on detailed auction
specific and firm level data. Based on the results, we measure the effects of competition
on the bidding behavior and compare bidding behavior before and during the economic
crisis. Our model permits quasi-experimental evidence on the effect of the crisis as well
as the government׳s stimulus in the construction sector. The pro-competitive effect from
free capacity and increased competition on the markup is estimated to be −1.5 percentage
points overall and −3.3 percentage points for winning bids. Our evidence suggests that the
fiscal stimulus, by injecting additional demand, counteracts the decline in markups. Thus,
from two pieces of evidence we consistently find procyclical markups. As our results are
based on careful structural modeling and detailed data, both auction specific and firm
specific, our results should not only contribute to research in industrial organization,
but could also be a useful input for macroeconomics to model the effects of activist
fiscal policy.


<h>REFERENCES</h>
----------

  [1] Susan Athey, Philip A. Haile. Chapter 60 Nonparametric Approaches to Auctions. doi:10.1016/S1573-4412(07)06060-6
  [2] Estelle Cantillon. The effect of bidders' asymmetries on expected revenue in auctions. doi:10.1016/j.geb.2006.11.005
  [4] Joachim R. Groeger. A Study of participation in dynamic auctions. doi:10.1111/iere.12085
  [5] Emmanuel Guerre, Isabelle Perrigne, Quang Vuong. Optimal nonparametric estimation of first-price auctions. doi:10.1111/1468-0262.00123
  [6] Han Hong, Matthew Shum. Increasing competition and the winner’s curse: Evidence from procurement. doi:10.1111/1467-937X.00229
  [7] Mireia Jofre-Bonet, Martin Pesendorfer. Estimation of a dynamic auction game. doi:10.1111/1468-0262.00455
  [8] Susan Athey, Jonathan Levin, Enrique Seira. Comparing open and sealed bid auctions: Evidence from timber auctions. doi:10.1093/qje/qjq001
  [9] Elena Krasnokutskaya. Identification and estimation of auction models with unobserved heterogeneity. doi:10.1093/restud/rdq004
  [10] Elena Krasnokutskaya, Katja Seim. Bid preference programs and participation in highway procurement auctions. doi:10.1257/aer.101.6.2653
  [11] Jean Jacques Laffont, Quang Vuong. Structural Analysis of Auction Data
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<ART>Decentralization and efficiency of subsidy targeting: Evidence from chiefs in rural Malawi
================================================================================

Authors: Maria Pia Basurto, Pascaline Dupas, Jonathan Robinson
DOI: 10.1016/j.jpubeco.2019.07.006
Year: 2020
ASJC codes: 2002, 2003
Keywords: Agricultural inputs, Chiefs, Nepotism, Political economy, Productive efficiency, Subsidies

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Lower-income countries spend vast sums on subsidies. Beneficiaries are typically selected via either a proxy-means test (PMT) or through a decentralized identification process led by local leaders. A decentralized allocation may offer informational advantages, but may be prone to elite capture. We study this trade-off in the context of two large-scale subsidy programs in Malawi (for agricultural inputs and food) decentralized to traditional leaders (“chiefs”) who are asked to target the needy. Using household panel data, we find that nepotism exists but has only limited mistargeting consequences. Importantly, we find that chiefs target households with higher returns to farm inputs, generating an allocation that is more productively efficient than what could be achieved through strict poverty-targeting. This could be welfare improving, since within-village redistribution is common. Productive efficiency targeting is concentrated in villages with above-median levels of redistribution.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Targeting programs such as subsidies to needy households is an important part of what
governments do. To do this effectively, governments must first identify who is truly
needy, which is difficult in developing countries where government infrastructure and
information technology are limited (particularly in rural areas). Governments typically
have the choice to administer such selection of eligibles centrally, or to decentralize
authority to local communities (usually these programs are officially administered by
local leaders).1 Decentralization has two main benefits: (1) local leaders are likely more
informed about the relative neediness of people in their village (especially in a context
in which most people do not file a tax return); and (2) local leaders will be more
accountable to villagers, particularly if leaders face village electoral pressure or are
motivated by reputation concerns. On the downside, decentralization may open the door for
corruption or nepotism. This paper uses rich panel data collected from a sample of 1559
households over four survey rounds in 2011–2013 to explore this fundamental trade-off in
the context of two subsidy programs in Malawi — the well-known farming input subsidy
program (FISP) which provides subsidies for fertilizer and hybrid seeds once a year, and a
one-time food aid relief program put in place after a financial crisis and drought in
2012. These programs were conceived as anti-poverty programs and the selection of
beneficiaries was decentralized to local traditional leaders, called chiefs. How well do
chiefs target the programs? This is a setting in which the trade-off between nepotism and
information could be severe. On the one hand, nepotism is possible since chiefs cannot be
held accountable via electoral pressure — in contrast to the contexts studied in Bardhan
and Mookherjee (2000, 2005) or Bardhan (2002), the position of chief in Malawi, as in many
other countries in the region, is hereditary and chiefs face fairly weak oversight. There
is also no strict eligibility rule provided by the government (only general guidance on
who should be “considered” for the subsidy) and no government back-checking of
allocations.2 But on the other hand, local information is critical, along two main
dimensions: (1) shocks occur frequently and chiefs likely have good information on recent
household-specific economic conditions; and (2) the return to inputs will likely be
heterogeneous across households within a village and related to factors such as household
demographics (especially in regards to availability of family labor), soil type, and
access to credit. Targeting inputs to those with the highest returns will increase total
village output by the most, and if ex post inter-household transfers can be used to
redistribute these gains, then targeting based on productive efficiency rather than
neediness may be Pareto-optimal. The paper answers two sets of questions. First, how
common are errors of exclusion (truly needy households not getting the subsidy) under the
status quo? Do chiefs use local information to target households which have suffered
recent negative shocks? Do they favor relatives? Second, do chiefs take into consideration
productive efficiency when allocating the input subsidies? Specifically, do they target
the agricultural subsidies to households with higher returns to fertilizer? To answer the
first set of questions, we use observed food expenditures in the immediate pre-subsidy
period as our measure of neediness, and benchmark the targeting effectiveness of the
chiefs against that of a counterfactual proxy-means test (PMT). We find evidence that both
the chiefs and the counterfactual PMT miss a substantial fraction of poor people, but that
the chiefs miss significantly more: chiefs make more and bigger errors. Specifically,
mean-squared error is 2–3.5 times higher for the observed allocation as for a
counterfactual PMT. We also find evidence of nepotism: chiefs are more likely to target
food subsidies to relatives. However, this nepotism appears to have minimal aggregate
welfare consequences, since chiefs' relatives are similarly poor as other villagers. We
also find that chiefs use their informational advantage to the benefit of households hit
with negative shocks: people who have experienced droughts, floods, cattle death, or crop
disease are significantly more likely to receive subsidies under the chief than under a
PMT-based allocation. The second part of the paper tests whether chiefs target input
subsidies to people with higher returns to agricultural inputs. The test is derived from a
model of subsidy allocation in which chiefs have preferences over households, but also
have information about household-specific returns to agricultural inputs. We assume that
there is little heterogeneity in productive returns to food, in which case the allocation
of the food subsidy is reflective of the welfare weights. To back out the relative
importance of productivity considerations in the chief's objective function, we exploit
the wedge between the allocations of the food and input subsidies. Taking this to the
data, we find that chiefs indeed allocate relatively more inputs to households with higher
gains from fertilizer use, while the PMT would not, suggesting productive efficiency gains
from a decentralized system.3 As predicted by the model, targeting based on gains to
fertilizer use is observed primarily in villages that exhibit above-median levels of
income-pooling: it is only if the extra production can be shared ex post through inter-
household transfers that targeting agricultural subsidies based on efficiency rather than
poverty considerations can be Pareto-optimal. Our paper paints a nuanced view of the
targeting of chiefs. On the one hand, we find evidence that decentralization has the
benefit of improved information on recipients.4 On the other hand, we do find evidence of
nepotism. As in Alatas et al. (2013), we find that the ultimate welfare consequences of
nepotism are likely small, however, since a PMT would not perform much better.5 The main
reason for this is that assets like land are noisy predictors of consumption in rural
Africa — the R-squared for our PMT regression is only 0.32, and we document similar
figures for datasets from Kenya and Uganda. This may be one reason why earlier work —
including several previous studies in Malawi (Dorward et al., 2008, 2013; Kilic et al.,
2013) had found higher levels of mistargeting and elite capture than we do: they used
assets as a proxy for need instead of consumption. Our paper makes several contributions
to the literature. Our core contribution is to bring attention to the difference between
poverty-targeting and poverty reduction (the ultimate goal of subsidy programs). In
communities with informal income-pooling, productive efficiency targeting may be the more
effective (albeit indirect) way of reducing poverty. For this reason, looking only at who
gets input subsidies rather than how the produced output is allocated is not sufficient to
gauge impacts on poverty alleviation. More broadly, we contribute to the literature on the
role of traditional authorities in African development. While survey evidence from the
Afrobarometer suggests that traditional leaders are perceived to regulate important
aspects of the local economy in numerous African countries (Logan, 2011; Michalopoulos and
Papaioannou, 2013), the question of whether their existence further undermines weak
governance, or instead palliates it, is still unsettled. Acemoglu et al. (2014) find that
areas of Sierra Leone where competition among potential chieftaincy heirs was low during
and after British colonial rule have significantly worse development outcomes today, but
higher levels of respect for traditional authorities. They hypothesize that this reflects
the ability of uncontested traditional ruling families to simultaneously capture resources
and civil society organizations. Our evidence from Malawi mitigates this view: in our
context, traditional leaders are uncontested and popular, as in Acemoglu et al. (2014),
but effective at targeting input subsidies to productive farmers, possibly putting their
village on a higher growth path.6 The layout of the paper is as follows. Section 2
presents some background on the Malawian local governance structure and decentralized
subsidy programs. Section 3 discusses the sample and data. Section 4 presents evidence on
poverty-based (mis)targeting. Section 5 tests for productive efficiency targeting. Section
6 concludes.

<hs>  Local governance in Malawi and the role of chiefs</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In Malawi, the democratically elected local government coexists with a traditional
chieftaincy hierarchy. There are four ranks within this hierarchy: Paramount Chief,
Traditional Authority (TA), Group Village Headman (GVH), and Village Headman (also known
as village chief). In our data, TAs have authority over areas smaller than a district.
They oversee from 10 to 45 GVHs, and GVHs oversee between 2 and 10 villages.7 Chiefs in
Malawi hold little formal power. They do not have direct control over any public funds and
are not allowed to raise local taxes. However, chiefs hold other customary
responsibilities. The 1998 Decentralization Policy and Local Government Act Malawi
Government (1998) recognized the rights of chiefs to allocate communal land and adjudicate
matters related to customary law (in particular customary land). Chiefs also play an
advisory and coordination role regarding local development projects. Finally — and this is
the focus of our paper — chiefs are typically relied upon to identify beneficiaries for
targeted government programs. Traditional leadership positions are hereditary, and chiefs
who pass away are replaced from within the chieftaincy clan. Chiefs are paid a salary by
the government that is known as mswahala, but it is fairly small.8 Chiefs do occasionally
charge fees to villagers (in our sample, 44% of villagers report having ever made a
payment to the village chief). Interestingly, chiefs are favorably viewed by the majority
of the Malawian population. In 2008–2009, 74% of Afrobarometer respondents in Malawi
perceived traditional leaders as having “some” or “a great deal” of influence, and 71%
thought the amount of influence traditional leaders have in governing the local community
should increase — for comparison, the average across 19 African countries for these two
questions were both 50% (Logan, 2011). Possibly as a result of this high popularity,
chiefs appear able to influence local villagers on whom to support in general elections
and local government elections (Patel et al., 2007), an influence that may limit their
accountability to elected representatives.

     <hss>Fertilizer subsidy program</hss>

        Malawi's Farming and Agricultural Input Subsidy Program (FISP) is one of the
        largest fertilizer and seed subsidy programs in the world.9 Though the program has
        existed since 1998, it greatly expanded after a drought in 2004 and steadily
        increased in size for a number of years after, until contracting more recently. In
        2012–2013, the program reached 4.4 million recipients and took up 10–15% of the
        government's budget (Dorward et al., 2013; Baltzer and Hansen, 2011). In our data,
        the percentage of people benefiting from subsidies has increased steadily over
        time, from 63% in 2008 to 82% in 2012. The subsidy program covers several inputs
        and comes in the form of vouchers, which are redeemable at local agricultural
        shops. The four items covered by the voucher subsidy during our study period were
        planting fertilizer (a 50-kilogram bag of NPK, worth about $40 at market prices in
        2013), top-dressing fertilizer (a 50-kilogram bag of Urea, comparable in price to
        NPK), hybrid maize seeds (a 5-kilogram bag, worth about $7), and hybrid groundnut
        seeds (a 2-kilogram bag, worth $2.60). The price of the voucher is only $1.7, so
        the subsidy was worth about 98% of the value of the input during this time period.
        As a result, take-up of the vouchers in our study sample is universal.10 There is
        no strictly defined, official eligibility criteria for the subsidy, but the
        intention is to target the poor and vulnerable. The official FISP guidelines reads
        that beneficiaries “will be full time resource poor smallholders Malawian farmers”
        but no threshold is provided for what defines “resource poor.” The program
        guidelines does hint at particular groups however: “...the following vulnerable
        groups should also be considered: elderly, HIV positive, female headed households,
        child headed households, orphan headed households, physically challenged headed
        households and heads looking after the elderly and physically challenged” (MoAFS,
        2009). Many of these targeted groups may have lower returns to inputs than the
        average poor household, for example because they are unable to farm intensively.
        The identification of beneficiaries has three main stages (Chirwa et al., 2010).
        First, the government conducts a national farmer registration census. Second, the
        central government allocates vouchers to districts as a function of the area's
        farming population and the acreage under cultivation.11 Finally, within each
        village, once the number of subsidies available to the village is known, a list of
        eligible villagers is made. Formally, the selection of beneficiaries at this stage
        is supposed to be done by a Village Development Committee through open community
        meetings, and audited by the DADO. However, as we will show below, most authority
        appears to be de facto delegated to chiefs.12 Once the list of beneficiaries have
        been received by the DADO, it establishes a date and venue for the distribution of
        the vouchers themselves. The distribution is done by a staff member from the DADO.
        Listed beneficiaries have to show their voter registration card in order to
        receive the vouchers and also to redeem the vouchers at the retail stores (MoAFS,
        2009). The identification of beneficiaries and distribution of vouchers is timed
        to precede the main rainy season (which runs from planting in November/December
        until harvest in April–August). During our study period, subsidy vouchers were
        distributed in September/October, in advance of planting.

     <hss>Food subsidy program</hss>

        Malawi devalued its currency in 2012, causing prices to rise 20–30% in 2012–2013
        (World Bank, 2015), which made food imports prohibitively costly. There was also a
        poor harvest in 2012, caused by a drought. In response, a food subsidy program was
        implemented in late 2012, lasting from November 2012 to January 2013. In our area
        of study, the subsidies were distributed in kind. As with the input subsidy, the
        program was targeted at the “poor” but without a precise threshold or formula for
        what constitutes poverty. Of those receiving the subsidy in our data, the average
        amount received was 103 kg of maize, 14 kg of soy blend, 18 kg of pigeon peas, 10
        kg of beans, and 3 L of oil. We estimate that this package was worth about $72 in
        2013 USD. As with the farming input subsidy program, chiefs were given primary
        responsibility for identifying which households would receive the food aid.

<hs>  Sample</hs>
  ~~~~~~

The data we use for this paper was collected as part of a separate randomized controlled
trial to estimate the impact of providing savings accounts to unbanked households (Dupas
et al., 2018, henceforth DKRU). The project took place around the catchment areas of NBS
bank branches in two districts of Southern Malawi — Machinga and Balaka. The sampling
frame for DKRU relied on a census of market businesses and a census of households
conducted at the end of 2010 — we use only the household sample for this analysis. The
household census listed 9297 households from 68 villages in three Traditional Authorities
(TA) areas: Kalembo, Sitola, and Nsamala. Of these, 78.8% met the eligibility criteria set
by DKRU: they did not have a bank account and had a female head of household. DKRU
randomly selected a subset of this sample for project inclusion, and completed baseline
surveys with 2107 households. This set of households is uses for the analysis in this
paper, though we must drop some households because their data is incomplete.13 We are
ultimately left with 1559 households in 61 villages for our analysis. Given this sampling
frame, our data departs from the universe of villagers in two ways. First, we
systematically excluded villagers who had bank accounts at baseline (which was about 15%
of the sample). These individuals are certainly richer than the average villager, and for
this reason our analysis may underestimate targeting errors (if any of the people with
bank accounts ended up receiving subsidies).14 Second, even among unbanked households, our
dataset includes only a subset of people in each village (roughly 10% on average).
However, since these villagers are randomly selected, our results are still internally
valid and of interest — our goal is to understand how chiefs allocated subsidies within
this sample, and our basic thought experiment is to ask what the gains would be from re-
allocating subsidies within this sample.

     <hss>Household panel</hss>

        We have four waves of survey data for each household: (1) a baseline conducted
        from February to March 2011; (2) a first follow-up survey conducted from February
        to March 2012; (3) a second follow-up survey conducted from September to December
        2012; and (4) an endline survey conducted from February to May 2013. The baseline
        survey includes a standard set of demographic variables, including a module on
        asset ownership which can be used to construct the allocation that would have
        obtained under a counterfactual allocation based on a proxy-means test from
        baseline assets. Each of these survey rounds included detailed expenditure
        modules. The follow-up and endline surveys include a module on the farming
        subsidy. This is used to construct a time series of subsidies received from 2008
        to 2013, for each household. The module includes information on which input
        subsidy was received, whether the household received the voucher itself or shared
        another household's voucher, and what the household actually did with the
        subsidized products (used them, sold them, shared them, etc.). The endline survey
        also asked these questions for the food subsidy, which was introduced in 2012.
        Finally, the endline included a separate module with questions on how the input
        and food subsidies were allocated. These include questions on how (in the
        respondent's opinion) the vouchers were allocated, whether a public meeting was
        held, whether the respondent participated in the meeting, etc. In addition,
        between August and October 2014 we collected a fifth wave of data for a random
        subset of 563 households in the initial sample. This survey asked additional
        questions on the process through which subsidies were allocated and on
        respondents' attitudes towards the allocation process as well as their perception
        of their chief's role, beliefs and objectives in this allocation. Importantly, we
        also elicited households' beliefs on the returns to farming inputs on their own
        land.

     <hss>Chiefs survey</hss>

        Between August and October 2014 we collected surveys with all of the 105
        traditional leaders in our study area of 61 villages, including 76 village headmen
        (chiefs) and 29 group village headmen (GVH).15 The survey included questions on
        their tenure and responsibilities, and included questions about the details of how
        the FISP and food subsidy programs were allocated. We also measured chiefs' self-
        reported awareness of whether some farmers had higher returns to inputs than
        others, and their knowledge of shocks encountered by villagers.

<hs>  Characteristics of households, chiefs and villages</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Table 1 presents basic summary statistics on the households in our sample. Panel A
includes time-invariant characteristics collected at baseline. The first variable shown is
the household's self-reported relationship to the chief. We asked the following question
to each respondent: “Are you related to the chief?,” to which 27% reported yes. In a
follow-up question, we asked: “How are you related?” The modal answer was the chief is an
uncle (20% of the related cases), followed by brother (13%), brother-in-law (12%) and
grandfather (12%). In what follows, we refer to those who reported as being related to the
chief as “kin”.16 Households in the sample are very poor: 90% have mud floors or worse
quality, 77% have thatch roofs, and less than 1% have electricity. Only 59% are literate,
and average years of education for the household head is just below 5.17 Twenty-eight
percent of households have no male head (most of these households are likely widows), and
97% own land. Panel B shows time varying expenditures, shocks and transfers. Across
rounds, households report spending only $9.66 per month per capita in total, and the
majority of this is on food ($6.80). These figures place these households well below the
global extreme poverty threshold of $1.25 per day. Shocks are also quite common: 26% of
respondents lost at least 1 day of work in the past month due to illness, 69% of
respondents experienced the sickness of another household member in the past month, 28%
experienced a drought or flood in the past 3 months, and 20% experienced crop loss or
livestock death in the past 3 months. Across survey rounds, 72% of households report being
worried about having enough food to eat in the past 3 months. Transfers across households
within the village are very common, with 58% of households reporting being recipients of
transfers in the last 90 days, and 25% reporting having made transfers. Columns 3 and 4 of
Table 1 show, for each variable, the gap between kin and non-kin and its standard error.
This reveals that if anything, kin are poorer than non-kin — they are significantly less
educated (Panel A), and have slightly lower consumption (Panel B). Lastly, Column 5 shows
the correlation between survey rounds for the variables in Panel B. This shows quite a bit
of variability over time — the inter-round correlation in food expenditures is only
0.35–0.43, suggesting that neediness varies over time. Table A1 presents summary
statistics on villages and village chiefs. The average village in our sample has 309
households and over 7000 acres of customary land. The average village chief is 53 years
old and has about 5 years of education. Eighty-two percent of chiefs are male. The average
chief has been in power for about 13 years, and 90% inherited the position (most of the
remainder were appointed). The vast majority faced no competition from within the family
blood line for the position. In principle, traditional leaders can be removed from office
or reprimanded, but our data suggests this almost never happens: only one chief reported
every being suspended. When chiefs were asked about their main responsibilities, the five
most common responses were resolving conflicts among villagers (90%), reporting issues to
higher level chiefs (61%), monitoring village projects (56%), disseminating information to
villagers (33%), and overseeing subsidy programs (20%).18

<hs>  Summary statistics on the allocation of subsidies in our sample</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Table A2 presents summary statistics on the process through which input and food subsidies
were allocated. Panels A and C rely on the latest round of survey data (2014) and presents
evidence on how both chiefs (Panel A) and villagers (Panel C) experience and perceive the
subsidy allocation mechanisms. Panel B presents data from the earlier household survey
waves. The data confirms that chiefs are the primary decision-makers in allocating
subsidies. Turning first to Panel A, the majority of village chiefs report that they have
control over the subsidy allocation: 62% declare that they decide by themselves, while an
additional 3% report that they decide in collaboration with others. Of the remainder, 13%
report that the village development committee (of which the chief is a member) decides the
allocation, and 13% report that subsidies are allocated in a village meeting (which the
chief typically runs). When asked about selection criteria, chiefs report need as the
primary criterion. Chiefs also put significant weight on female-headed households,
households which recently received a shock households taking care of orphans, and
households that the chief believes are hard-working. Panel B shows that community meetings
regarding selection happen quite regularly: 95% of villagers report that a meeting was
held, and 82% report attending this meeting for FISP (65% attended in regards to the food
subsidy). Consistent with chief responses in Panel A, households responses in Panel C
confirm that the chief is mostly responsible for allocating the subsidies — 72% report
that the chief decides alone (49%) or with others (23%) on the input subsidies, and 73%
report that the chief alone decides on the food subsidies. Households report similar
inclusion criteria as do chiefs (needy households, as well as elderly and female-headed
households). While official FISP guidelines do not endorse sharing of subsidy packages, we
find strong evidence that sharing is in practice very common (Web Appendix Table W1).
Seventy-seven percent (0.46/0.60) of households who received an input subsidy voucher
report sharing it. Moreover, we find that sharing is often at the direction of the chief:
of those who shared, 83% say they received instructions from the chief on whether to share
it, and 79% received specific instructions from the chief on whom to share with. Food
subsidies are similarly shared.19 In what follows, we perform all analyses considering
both allocations: the allocation of the vouchers themselves, and the allocation observed
after sharing (we call this the “realized allocation”).20

<hs>  Measuring neediness</hs>
  ~~~~~~~~~~~~~~~~~~~

To measure neediness, we use food expenditures, which we consider a proxy for consumption.
Food expenditures have been shown to be better predictors of neediness than other measures
such as income (Deaton, 1997; Meyer and Sullivan, 2012). While we measured expenditures on
12 broad food categories (covering all food types), in the main analysis we focus on the
10 categories that are typically purchased rather than self-produced.21 These 10
categories are vegetables, fruits, meat, dairy/eggs, salt, sugar, other cooking items
(oil, margarine), coffee and tea, snacks, and juice/sodas. We compute the sum of
expenditures on these 10 food categories over the 30 days preceding the survey and then
divide the sum by the number of household members to construct “per capita non-staple food
expenditure” or PCF, our measure of need going forward (we report this figure in USD).22
The distribution of log PCF in our data is plotted separately for the two main years of
analysis, 2011 and 2012, in the top panel of Web Appendix Fig. W.

     <hss>Timing</hss>

        The food expenditure we would ideally use to determine “true need” (PCF
        eligibility) would be measured at the time that subsidy beneficiaries are
        identified (which is around August for the input subsidy and November for the food
        subsidy). The timing of our surveys does not precisely correspond to these
        periods. Our food expenditure module covered the last 7–30 days (depending on the
        question) before the survey date. Thus, given the dates of the surveys mentioned
        in Section 3.2, we have consumption data for the following periods: January 2011
        to February 2011; January 2012 to February 2012; August 2012 to November 2012; and
        January 2013 to April 2013. To study the targeting of the 2011 input subsidy, we
        thus have to rely on the January 2011 to February 2011 expenditure data, which is
        substantially before the period of interest. In particular, it is before the March
        2011 harvest, which is likely an important determinant of actual neediness as of
        August–November 2011.23 Fortunately, the data used for the 2012 subsidies is for
        the correct time period (August to November). For this reason, our 2012 results
        are our preferred estimates.

     <hss>PMT score rank</hss>

        To construct the counterfactual in which subsidies were allocated via PMT, we
        repeat this procedure but this time we rank households (within each village) by a
        “PMT score.” We compute the PMT score as follows: we regress log PCF on household
        characteristics, including demographic characteristics, dwelling characteristics,
        assets and occupation, and use the estimated coefficients to predict a score for
        each household. As in Alatas et al. (2012), we do this in two steps: we first run
        kitchen sink regressions with all available characteristics and then, using a
        backward step-wise procedure, keep only those characteristics which are
        statistically significant at the 10% level. PMT regressions are shown in Table A3.
        We show the results for both per capita and per adult equivalent food expenditure,
        and find slightly higher predictive power for per capita values.24 From Column 1,
        we obtain a R-squared of 0.32, which is somewhat lower than the 0.40 obtained by
        Alatas et al. (2012) in Indonesia (when pooling districts together).25 For
        comparison, we also construct a PMT score using data from the 2010–2011 wave of
        the Integrated Household Survey (IHS3), a representative household survey
        collected by Malawi's National Statistics Office. We restrict that dataset to the
        two districts in our sample, and estimate PMT regressions using the same backward
        step-wise method to identify covariates. Results are shown in Web Appendix Table
        W2. In the table, we run regressions separately where we restrict to only those
        variables which were also collected in our surveys (which we call “BDR
        variables”), which are shown in Column 1, and for all potential covariates
        available in the IHS3 (Column 2). We find R-squared statistics in both regressions
        of approximately 0.4. We conjecture that the somewhat lower R-squared we observe
        in our own survey data is because our sample is somewhat poorer than a
        representative sample, and their consumption may be more volatile due to lower
        access to insurance. To shed some light on this, we run similar regressions in
        samples of unbanked households we have collected in other work in Kenya (Dupas et
        al., 2019) and Uganda (Dupas et al., 2018). We find an R-squared of 0.31 in Kenya
        and 0.28 in Uganda.

        PMT vs. chief allocation

        Our first set of results is shown in Fig. 1, which plots the probability of
        receiving the subsidies by quintile of the PMT score distribution (top panel) and
        quintile of the PCF distribution (bottom panel). These quintiles are across the
        entire sample, and so include across-village variation. We show the realized
        allocation (i.e. the allocation after vouchers were shared) as well as two
        counterfactual allocations: the PMT allocation, our “benchmark” for what could be
        done under centralization; and the PCF-based allocation, the “optimal” allocation.
        We pool across villages, which vary in their underlying distributions as well as
        in the number of subsidies available, which explains why neither of the two
        counterfactual allocations are perfect step functions of their respective
        distributions. It also explains why even the PCF-based allocation in Fig. 1 does
        not reach perfect targeting: there is mistargeting of the number of subsidies
        across villages, which means that even a perfect allocation within village would
        yield evidence of mistargeting. The gradient in the PCF-based allocation in Fig. 1
        should therefore be considered as the “best possible targeting” given the across-
        village allocation in our data.26 From the top panel of Fig. 1, it is clear that
        chiefs target different people than the PMT would: while the PMT, by definition,
        would allocate subsidies to 100% of people at the bottom of the distribution, the
        chiefs' allocation has a much flatter gradient with respect to the PMT score. In
        isolation, this result looks similar to Dorward et al. (2008, 2013) and Kilic et
        al. (2013), who look at how well chiefs target based on assets and conclude that
        there is widespread mistargeting. The bottom panel of Fig. 1, which show targeting
        based on PCF, also show that the PMT does better than chiefs — but the gap is much
        smaller than in the top panel. In the allocation decision of 2011 (which was
        contemporaneous to the survey from which the PMT was calculated), the gradient for
        the PMT allocation is quite a bit steeper than that of the chiefs, but by 2012 the
        slopes are more similar. This could be because characteristics measured in 2011
        become less and less predictive as time goes on, and might suggest that the
        advantage of a PMT may be short-lived. Fig. 1 also shows that the PMT makes a
        substantial number of errors. This is true even if we use the PMT formula from the
        IHS3 rather than the one derived in our dataset. The relatively poor targeting
        performance of the PMT seems due to the fact that assets (the most important
        factor in the PMT) are a relatively poor proxy for need in our study context,
        because PCF eligibility is not time-invariant (the correlation between food
        expenditures across rounds is only 0.35 as previously discussed and shown in Table
        1) and because there are important unobservables in the determinants of PCF. In
        Fig. 2 we show the allocation against the PCF quantile, both before and after
        sharing. Before sharing, just over 50% of households received the input voucher
        and 34% received the food voucher; after sharing, these percentages increase to
        about 78% and 59%. However, poverty-targeting efficiency does not improve from
        sharing: Fig. 2 shows that the slope of the realized allocation is identical to
        the slope of the initial voucher allocation, suggesting that the sharing happens
        primarily within quantile of the PCF rather than across.

     <hss>Error rates</hss>

        Table 2 shows the average village error rate (averaging first over individuals
        within villages, and then across villages) under the two allocation schemes
        (chiefs and PMT). For these calculations, we include only those villages in which
        the probability of getting a subsidy is between 0 and 100% (so that targeting
        errors are possible).27 The poverty-targeting error rate is the probability that a
        household is (1) eligible based on its position in the PCF distribution within the
        village; but (2) does not make it onto the actual beneficiary list (chief error)
        or on the counterfactual PMT beneficiary list (PMT error). Note that since the
        number of beneficiaries within the village is kept fixed in this exercise, this
        error rate also provides the probability that a household is (1) categorized as
        ineligible based on its position in the PCF distribution and (2) gets the subsidy.
        In other words, mechanically there are as many people who don’t get the subsidy
        when they should (exclusion errors) as there are people who get the subsidy when
        they should not (inclusion errors). We also show what the expected error rate
        would be if subsidies were allocated randomly. These are calculated from a
        permutation test with 1000 draws. Finally, we also compute the squared error for
        each allocation. We can see that both allocations make a significant number of
        errors compared to the PCF-based allocation, but that the PMT always has a lower
        error rate. The error rates for chiefs is 15.8% and 14.4% for the 2011 and 2012
        input subsidies, while the PMT's error rate is only 10.3% and 10.9%. For the food
        subsidy, the chief's error rate is 15.1%, compared to 13.7% for the PMT. Since not
        all errors are equally important (i.e. denying a subsidy to somebody just barely
        under the threshold is not nearly as costly as denying a very poor person), a more
        informative measure of errors may might be the mean-squared error (shown in the
        bottom of the table). Here too we see consistent evidence that the PMT has a lower
        MSE than do chiefs, across all subsidies types. Finally, we see that the PMT based
        on our data does consistently better than that based on the IHS3; however, both
        outperform the chiefs' allocation. While chiefs do worse than the PMT, they do
        better than random (see Table 4). For the input subsidy, the simple error rate for
        chiefs is not statistically distinguishable from random, but the mean squared
        error is much lower, suggesting that chiefs trade PCF eligible for ineligible only
        around the PCF cutoff. Chiefs also do better than random on the food subsidy, by
        both metrics (Table 2). An interesting pattern in these results is that, compared
        to the PMT, chiefs look worse at targeting the truly needy for the input subsidy
        than for the food subsidy. A central hypothesis of this paper is that this may be
        due to productivity targeting of the input, which we will argue is less relevant
        for food. We dive into this issue in detail in Section 5.

        Who is favored and who is left out by chiefs?

        Table 3A shows the results of a multivariate regression of the realized allocation
        (i.e. receiving a voucher or a share of a voucher) on background characteristics
        and village fixed effects. Columns 1–4 show regressions for the real-life
        allocation (decided by chiefs) while Columns 5–8 show a counterfactual allocation
        if the subsidies were allocated by the PMT formula. Table 3B performs the same
        analysis, but for receiving the voucher itself (i.e. not including people who
        received the subsidy via sharing). Comparing the coefficient estimates across the
        three sets of analyses tells us who is favored and who is left out under each
        scheme. We consider both the extensive margin (receiving any subsidy) and the
        intensive margin (the value of the subsidy received, since this varies across
        households due to sharing).28 The first row of Table 3A confirms the poverty-
        targeting results discussed above: the gradient in PCF is more negative under the
        PMT than under the chiefs, and the gap in the gradient is more pronounced for the
        input subsidy than for the food subsidy. We find evidence of nepotism: conditional
        on covariates, chief's kin are 11 percentage points more likely to receive the
        food subsidy under the chief, whereas they would not be favored under the PMT. For
        the input subsidy, nepotism appears much less pronounced: while chief's kin
        receive a greater input subsidy package (an extra 3.30 kg compared to a mean of
        50.5 kg, significant at 10%), the PMT would also award kin higher subsidy packages
        (+2.3 kg, also significant at the 10% level). This is due to the fact that chiefs'
        kin are marginally asset poorer than non-relatives. Turning to other covariates,
        we find that chiefs target older households, as per the official FISP
        recommendation. Chiefs also target households that received negative shocks:
        households who experienced a drought or flood are 4 percentage points more likely
        to receive subsidized food, while households who experienced crop loss or cattle
        death are 8 points more likely to get it. By contract, the PMT is not designed to
        respond to shocks, and indeed we find no correlation between shocks and subsidy
        receipt in the PMT (such a correlation might exist if shocks are strongly
        correlated with asset poverty).

<hs>  Discussion of poverty-targeting results</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The results in Tables 3A and 3B epitomize the trade-off between local information and
capture: we find that chiefs are able to use local knowledge to benefit households hit by
recent negative shocks, while the PMT misses them; but they also favor their kin. These
results raise several questions. First, is the fact that kin are more likely to get
subsidies evidence of nepotism? An alternative hypotheses is that chiefs have better
information on relatives, and therefore are more likely to target kin because they can be
certain that they are truly poor. If this is the case, we would expect that subsidies to
kin would be more responsive to consumption than to non-relatives. We investigate this in
Table A4, in which we include an interaction between log food and kinship. We find no
evidence in favor of the information hypothesis: targeting actually appears somewhat worse
for relatives for the input subsidy, though there is no effect for the food subsidy. We
also do not find that targeting based on shocks is better among relatives (Table A4),
consistent with the fact that kin are favored irrespective of whether they faced a shock.
While we lack data to definitively rule out an information story, our evidence appears
more consistent with nepotism.

<h>PRODUCTIVE EFFICIENCY TARGETING</h>
-------------------------------

In this section, we investigate whether some of the apparent mistargeting of input
subsidies by chiefs is due to targeting on farming productivity: if returns to input
subsidies are heterogeneous and chiefs have information on this, then they might allocate
subsidies in a way that takes both poverty-targeting and productive efficiency into
account. We use a simple model that allows for heterogeneity in returns as well as
heterogeneity in the welfare weights that chiefs assign to households, to derive a test of
whether the mistargeting we observe for input subsidies is in part driven by productive
efficiency considerations.

<hs>  Model and prediction</hs>
  ~~~~~~~~~~~~~~~~~~~~

We consider the problem of allocating subsidies across households within a village. The
intra-village allocation is done by the village chief. This leads us to the prediction we
can test in the data:

     <hss>Allowing chiefs to orchestrate transfers</hss>

        Productive efficiency considerations when allocating farming subsidies increase as
        the level of ex post income-pooling in the village increases. Prediction 2 brings
        attention to the fact that the two subsidies we study could be complementary: the
        input subsidy as a growth instrument and the food subsidy as a redistribution
        instrument. This logic could also imply that the food subsidy and input subsidy
        allocations could be related — farmers who received the input subsidy should have
        larger harvests and be less in need of the food subsidy. Note that this does not
        invalidate our test: the food subsidy should be allocated based on Pareto weight
        and current consumption, irrespective of whether the current consumption level was
        secured through enhanced yields in the previous period thanks to inputs subsidies
        or not. Relative Pareto weights can still be backed out from jointly observing the
        food allocation and current consumption, as we do.31 Below we show that our
        predictions hold under a number of extensions to the basic model.

<hs>  Results</hs>
  ~~~~~~~

To test predictions, we need a measure of A, the household-specific (farm-specific)
productivity of fertilizer. In this or any context, estimating the productivity of an
input is very difficult, since input choices are endogenous and farmers with higher
returns are presumably more likely to use fertilizer in a given season. Returns are also
volatile across years and even within farms, so estimating this well would typically
require a long panel. Instead of estimating productivity, we therefore opted to simply ask
farmers for their expectations of yields with and without fertilizer use. We collected
this data in the fifth survey round conducted in the summer 2014. There are several
important caveats. First, due to budget constraints the survey could only be done with a
random subset of households in each village. The sample includes only about one third of
the sample. Second, the questions are about total output with and without fertilizer,
rather than marginal returns.32 We show the means of the reported expected yield in Panel
C of Table 1, and we plot the distribution of the reported gain in total output in Panel B
of Fig. W in the Web Appendix. There is substantial heterogeneity in these reported gains
from input use. What drives it? Table A5 examines correlates of self-reported gains. We
regress the reported log yield increase on log acres and other observables. We find that
reported gains are correlated with many variables, including household demographics (gains
are increasing in the age of the head of household), education, log assets, and household
size (though this is not statistically significant). We expect that these are the types of
proxies that the chief may use to target subsidies, in addition to other characteristics
that are unobservable to us, such as land quality. Also of note is that the correlation
between estimated production gains from using fertilizer and our measure of neediness,
PCF, is fairly weak (Panel C of Fig. W). We also find no systematic differences by kinship
status (Table 1 Panel C, column 3, and Table A5). These results are in sharp contrast with
those for the counterfactual PMT distribution, in which the value of the subsidy is
actually (insignificantly) declining in the gains to fertilizer (because of a negative
correlation between returns and assets). In that case, the PMT undermines the effect of
the subsidy on total farm output at the village level. In contrast with the chief's
allocation, the gap between fertilizer and food subsidy values does not significantly
increase with reported gains from fertilizer under the PMT allocation (Table 4, column
6).33 Overall, the results in Table 4 and Fig. 3 are consistent with chiefs taking
productive efficiency into consideration when allocating input subsidies — something that
the PMT cannot do since information on who has more to gain from fertilizer use is not
something that can be elicited in an incentive-compatible way if people expect their
subsidy package to depend on it. The magnitude of the effects is not trivial: a household
with an extra log point gain from fertilizer gets about 6.5 more kgs of input subsidies
under the chiefs than under the PMT.

<hs>  Supportive evidence</hs>
  ~~~~~~~~~~~~~~~~~~~

Is information on the relative productivity of various potential beneficiaries of the
input subsidy embedded in the chief, or does it rest in the people themselves? People who
have high value for the input subsidy could wait in line more, lobby more or protest more
if they don’t get the subsidy, such that the allocation of the chief ultimately favors
them in a way that looks as if the chief himself were aware of the heterogeneity. To
provide descriptive evidence on this question, in the 2014 survey, we asked respondents if
they had ever lobbied the chief to obtain subsidies. Only 9% of respondents reported
lobbying for input subsidies, and 4% reported lobbying for food subsidies (Table W1). The
likelihood of having lobbied is not positively correlated with returns to fertilizer for
the overall sample (see Table 4, column 7), though it is correlated among the chiefs' kin
(see Table A6, column 7). However, we argue that the this lobbying is of modest
importance, since kin lobby much less on average, and overall the targeting efficiency is
not higher among kin as shown in Table A6 columns 1–3. In the survey of chiefs also
conducted in 2014, we asked chiefs a number of questions about what they could observe
about households, which we present in Web Appendix Table W7. We find that 86% of chiefs
report that they can easily categorize farms in their village in terms of productivity of
inputs. Chiefs also report that they know who works harder, who has money for inputs, and
whose returns are highest. While descriptive, these responses are consistent with chiefs
having significant local knowledge.

<hs>  Threats to validity</hs>
  ~~~~~~~~~~~~~~~~~~~

In this section, we discuss several possible threats to internal validity: (1) the fact
that returns to inputs are self-reported rather than observed, and (2) the fact that the
two subsidy programs we consider exist alongside other social programs which may be
allocated simultaneously.

     <hss>Using self-reported returns</hss>

        A possible concern with our analysis is that returns are self-reported rather than
        directly observed, and so could potentially be correlated with various omitted
        variables. We present several pieces of evidence to help address this. First, we
        use our data to construct an agricultural panel. Specifically, we have complete
        data for the 2010–2011 and 2011–2012 planting seasons in this paper. From this we
        have at most 2 observations on households about their fertilizer use and output.
        We utilize this by running fixed effects regressions of output on input usage —
        relying on variation in input usage that occurs over years. The key variable in
        this regression is an interaction between self-reported gains and input usage — if
        the measure is valid, then this correlation should be positive. We show results in
        Table A7. We find strong evidence that these (admittedly non-random) returns to
        fertilizer are higher for those with higher self-reported returns. While we do not
        want to make too much of this since input usage is potentially endogenous, this
        fixed effects specification does rule out some time-invariant sources of bias —
        for example, land size and household demographics are held fixed in this analysis.
        At least descriptively, these results seem to support our interpretation. Beyond
        these results, we argue that many (though not all) stories for why households
        might get more subsidies would apply to both food and fertilizer subsidies. For
        example, one might argue that people with higher returns are more confident and
        have higher social status and are therefore more likely to get subsidies. But
        these sorts of stories would not explain our results, since these households would
        get more fertilizer and food, whereas our main empirical tests are about the
        difference in the value of the two types of subsidies. We also find that this
        relationship is stronger in villages with higher levels of sharing. While this is
        consistent with the framework we have written down, it does not seem likely that
        we would observe this particular pattern (which was derived ex ante) if the
        results were driven purely by omitted variables.

     <hss>Other safety net programs</hss>

        Beegle et al. (2017) document that chiefs are also involved in deciding which
        households are eligible for Malawi's public work program (PWP) — though the
        responsibility falls more on the Group Village Headmen and the villagers
        themselves. They report that Malawi's PWP “has been operational since the
        mid-1990s and aims to provide short-term labor-intensive activities to poor, able-
        bodied households for the purpose of enhancing their food security.” While we did
        not collect data on participation in the PWP directly from respondents in our
        surveys, a fuzzy name match between the original household sample and
        administrative data on PWP participants obtained from the two districts in our
        sample yields 167 matches for the 2012–2013 budget year, out of 2107 households in
        the DKRU baseline survey, suggesting that the PWP coverage in our study area is
        about 8%. Verification surveys with a subset of those matched and unmatched
        conducted in March 2015 suggests that an additional 3% may have been participating
        in PWP, bringing our estimates to roughly 11%.35 While name matching is always
        prone to significant error, this ballpark figure is not far from the 15% coverage
        targeted by the program. While studying how the PWP is targeted and the specific
        role of chiefs would have been interesting, omitting it due to data limitations
        should not affect our analysis of the other subsidy programs. Notably, Beegle et
        al. (2017) find no correlation between receipt of PWP and receipt of other
        benefits, suggesting no “fairness norm” influencing distribution across programs,
        in particular, no compensation of non-PWP households with input or food subsidies.

<h>CONCLUSION</h>
----------

Traditional leaders, often known as “chiefs,” have maintained a significant amount of de
facto if not de jure power in sub-Saharan Africa. Possibly owing to the weakness of local
governance in most of the continent, chiefs are commonly involved in the decisions of how
to allocate government resources. One prominent type of resource is subsidies. Developing
country governments allocate an important portion of their national budget to subsidies
targeted at the poor, and it is common for chiefs to be asked to identify who should be
eligible for such subsidies. Do chiefs identify the right beneficiaries? Previous work on
this question in Malawi concluded that there was widespread elite capture (Dorward et al.,
2008; Kilic et al., 2013), based on evidence that “connected” households are more likely
to receive subsidies, and that household assets measures do not strongly predict subsidy
receipt. We show that such evidence may not directly speak to the issue of poverty-
targeting in environments where assets are a poor predictor of need, and where the
subsidized items are productive inputs. We find evidence that chiefs allocate input
subsidies to farmers with larger returns to input use. This result underscores how a naive
measure of targeting based solely on the neediness of households (even when neediness is
well measured) may understate the poverty-alleviation impacts of the allocation: when ex
post redistribution is possible through informal transfers, targeting input subsidies
based on productive efficiency (i.e. using input subsidies as a growth instrument) can
have a larger impact on aggregate welfare than targeting based on poverty would. This
issue has not received much attention in the literature up to this point, even though most
of the inputs subsidized by governments are productive (farming inputs, health products)
that have heterogeneous returns. Future work should explore whether our results generalize
to other contexts and countries.


<h>REFERENCES</h>
----------

  [1] Daron Acemoglu, Tristan Reed, James A. Robinson. Chiefs: Economic development and elite control of civil society in sierra leone. doi:10.1086/674988
  [3] Vivi Alatas, Abhijit Banerjee, Rema Hanna, Benjamin A. Olken, Julia Tobias. Targeting the poor: Evidence from a field experiment in Indonesia. doi:10.1257/aer.102.4.1206
  [5] Pranab Bardhan. Decentralization of governance and development. doi:10.1257/089533002320951037
  [6] Pranab Bardhan, Dilip Mookherjee. Capture and governance at local and national levels. doi:10.1257/aer.90.2.135
  [7] Pranab Bardhan, Dilip Mookherjee. Decentralizing antipoverty program delivery in developing countries. doi:10.1016/j.jpubeco.2003.01.001
  [8] Pranab Bardhan, Dilip Mookherjee. Pro-poor targeting and accountability of local governments in West Bengal. doi:10.1016/j.jdeveco.2006.01.004
  [9] Kathleen Beegle, Emanuela Galasso, Jessica Goldberg. Direct and indirect effects of Malawi's public works program on food security. doi:10.1016/j.jdeveco.2017.04.004
  [14] Pascaline Dupas, Dean Karlan, Jonathan Robinson, Diego Ubfal. Banking the unbanked? Evidence from three countries. doi:10.1257/app.20160597
  [15] Pascaline Dupas, Anthony Keats, Jonathan Robinson. The effect of savings accounts on interpersonal financial relationships: Evidence from a field experiment in rural Kenya. doi:10.1111/ecoj.12553
  [20] Bruce D. Meyer, James X. Sullivan. Identifying the disadvantaged: Official poverty, consumption poverty, and the new supplemental poverty measure. doi:10.1257/jep.26.3.111
  [21] Stelios Michalopoulos, Elias Papaioannou. Pre-colonial ethnic institutions and contemporary African development. doi:10.3982/ECTA9613
<ART>Discounting by committee
========================

Authors: Antony Millner, Geoffrey Heal
DOI: 10.1016/j.jpubeco.2018.09.005
Year: 2018  |  Pages: 91-104
ASJC codes: 2002, 2003
Keywords: Collective decisions, Intertemporal choice, Social discounting, Time inconsistency

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We study a dynamic social choice problem in which a sequence of committees must decide how to consume a public asset. A committee convened at time t decides on consumption at t, accounting for the behaviour of future committees. Committee members disagree about the appropriate value of the pure rate of time preference, but must nevertheless reach a decision. If each committee aggregates its members’ preferences in a utilitarian manner, the collective preferences of successive committees will be time inconsistent, and they will implement inefficient consumption plans. If however committees decide on the level of consumption by a majoritarian vote in each period, they may improve on the consumption plans implemented by utilitarian committees. Using a simple model, we show that this occurs in empirically plausible cases. Application to the problem of choosing the social discount rate is discussed.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Suppose that a society needs to decide on an intertemporal consumption plan for some
public asset. A committee is convened at each point in time, and tasked with determining
how much to consume in the current period. The members of each committee have differing
opinions about the pure rate of social time preference (PRSTP), or utility discount rate,
that should be applied to this problem. Some favour a high discount rate, while others
believe that different time periods should be treated more equally, and thus favour a low
discount rate. Moreover, the current committee knows that future consumption choices will
also be made by committees exhibiting similar disagreements on discount rates. How should
such committees proceed, given the heterogeneity in opinions on discount rates? Although
it may seem abstract, this question is inspired by an important practical problem in
public economics: how should governments discount future utilities when evaluating public
policy decisions? The appropriate normative value of the PRSTP has been debated at least
since Ramsey’s (1928) seminal work on optimal national savings. Subsequent commentators
have argued the merits of a variety of values for the PRSTP without a clear ‘best’ value
emerging, and different governments have adopted different values for public decision-
making. The social time preferences economists prescribe for public decision-making today
are still highly heterogeneous (Arrow et al., 2013). This has been highlighted by the
long-standing debate about the appropriate value of the PRSTP for the evaluation of
climate change policies (Nordhaus, 2008; Stern, 2007). A recent survey of experts on
social discounting (Drupp et al., forthcoming) shows significant variation in their
prescriptions for the PRSTP (see Fig. 2). Given the persistent normative disagreements
about the PRSTP, it is natural to ask whether methods from social choice theory can be
used to obtain a compromise between opposing viewpoints. In this paper, we examine perhaps
the most common such methods: utilitarian aggregation and majoritarian voting. Under the
utilitarian approach, committees seek to maximize a weighted sum of the time preferences
advocated by their members in each period, while under majoritarian voting, committee
members vote on the current level of consumption, and a Condorcet winner (if it exists) is
implemented. The utilitarian approach is appealing, as Jackson and Yariv (2015) have shown
that any social choice rule that is non-dictatorial (i.e. sensitive to the preferences of
more than one individual) and respects unanimity (roughly, if everyone prefers consumption
stream C to C′ then C is socially preferred to C′) is equivalent to utilitarianism in the
setting we study. However, while no-dictatorship and unanimity are compelling properties
in isolation, they lead to a time inconsistency problem when combined with another
assumption: time invariance (i.e. preferences over future consumption streams are
identical in all time periods). Millner and Heal (2018) have argued that while time
invariance is an excessively strong assumption in intra-group intertemporal decision
problems (e.g. allocation between family members), it is plausible when modeling inter-
group choices like those facing the successive committees studied in this paper. Thus, if
a utilitarian approach to resolving disagreements is adopted, the collective preferences
of successive committees will conflict with one another. Rational utilitarian committees
will anticipate the actions of future committees, and react optimally to them, inducing a
dynamic game between committees. The equilibrium of this game will be seen as inefficient
by every committee. The inefficiency of the consumption path implemented by utilitarian
committees means that it is possible that voting could give rise to superior outcomes. If
each committee holds a majoritarian vote on the level of current consumption, and members
of the current committee rationally anticipate the outcome of future votes, we show that
the equilibrium consumption path under voting will correspond to the optimal plan of the
median member. Further analysis shows that a majority of committee members will prefer
this voting equilibrium to the utilitarian equilibrium, regardless of the choice of
aggregation weights in the utilitarian objective function. We extend this result to
welfare comparisons, finding conditions on the distribution of PRSTPs under which the
voting equilibrium is superior to the utilitarian equilibrium according to utilitarian
committees' own objective functions. Using survey data on economists' recommended values
for the PRSTP, we show that these conditions are often satisfied in practice. There is
thus a sense in which voting may be ‘self-stable’ (Barbera and Jackson, 2004) relative to
utilitarianism: a majoritarian vote between voting and utilitarian aggregation of PRSTPs
will always lead to voting being adopted as the aggregation method. By contrast, a
utilitarian comparison of voting and utilitarian equilibria will often favour voting. The
paper is structured as follows. We discuss related literature next, before developing our
simple model of dynamic public choice with disagreements about the PRSTP in Section 2.
This section contains the bulk of our analysis. We first derive the equilibrium behaviour
of utilitarian committees, and show that they choose inefficient consumption paths. Next,
we derive the equilibrium behaviour of committees that vote on consumption. Finally, we
contrast these two preference aggregation methods, deriving results on committee members'
ordinal preferences between the implemented equilibria, and comparing them from the
perspective of utilitarian committees' own collective preferences. Section 3 discusses the
results, and draws some lessons for the choice of the PRSTP in social discounting
formulae.

<hs>  Related literature</hs>
  ~~~~~~~~~~~~~~~~~~

The literature on aggregation of opinions about social discount rates stems from the work
of Weitzman (1998, 2001), who focuses on aggregation of expert opinions on real (i.e.
consumption) discount rates, rather than pure time preferences. Weitzman takes a sample of
opinions as to the appropriate (constant) real discount rate for project evaluation,
treats these as uncertain estimates of the ‘true’ underlying rate, and takes expectations
of the associated discount factors to derive a declining term structure for the ‘certainty
equivalent’ real discount rate. As Freeman and Groom (2015) observe, opinions about real
discount rates conflate ethical views about welfare parameters such as the PRSTP with
empirical estimates of consumption growth rates — they mix tastes and beliefs (see
Dasgupta, 2001 , pp. 187–190 and Gollier, 2016 for further discussions of Weitzman's
approach). This suggests that it is important to pursue approaches that treat preference
aggregation as a distinct problem. Our work highlights difficulties that may arise in
practice when decision-makers with a distribution of ethical views attempt to form
consensus social preferences, and contrasts the equilibrium outcomes that arise from
standard preference aggregation methods. The possibility that utilitarian preference
aggregation could lead to time inconsistency when agents favour different values of the
PRSTP has been noted by several authors (Marglin, 1963; Feldstein, 1964; Jackson and
Yariv, 2015). Millner and Heal (2018) argue that, while this is not a generic feature of
utilitarianism as an normative theory (see also e.g. Hammond, 1996), as a positive matter
it is likely to occur when distinct groups of agents are tasked with decision-making in
each time period, as occurs in the setting we study here. Our work thus falls somewhere on
the boundary between normative and positive analysis: we study positive properties of the
equilibrium consumption choices that would be implemented by sequences of committees that
seek to aggregate their members' normative views on social time preferences. Alternative
approaches to the aggregation of time preferences are pursued by Gollier and Zeckhauser
(2005), Jouini et al. (2010), and Millner (2018).

<h>THE MODEL</h>
---------

We focus on a sequential social choice problem in which a sequence of committees, each
composed of N > 1 members indexed by i = 1…N, must choose how to consume a public asset.
For the sake of analytical convenience, we assume that N is odd, and that time is
continuous. Each committee exists for a single moment in time, and controls the value of
consumption in that moment alone. Committee members are drawn from a stable population at
each moment, and their tenure lasts for only that moment. The distribution of members'
opinions on the PRSTP is assumed to be independent of time.1

<hs>  Utilitarian aggregation</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

To determine the limit equilibrium, we must find the linear MPE of the dynamic game
between committees. A Markovian strategy in our context is a function σ(S) such that
consumption at time t is given by Ct = σ(St) for all t ≥ τ. A strategy σ(S) is an MPE if,
in the limit as ϵ → 0, when committees at times t ∈ [τ + ϵ,∞) in the future use the rule
σ(S), the best response of the current committee in t ∈ [τ,τ + ϵ) is also to use σ(S). An
MPE is linear if the equilibrium strategy is of the form Ct = σ(St) = ASt for some A > 0.
The next proposition characterizes the limit equilibrium of the game between committees:
The possible non-existence of a linear MPE (and hence a limit equilibrium) when η < 1 is a
well known feature of models like ours (see e.g. Phelps and Pollak, 1968). To avoid
existence problems, we assume that η ≥ 1 in the remainder of the paper.6 From the
perspective of a committee in any period τ, the equilibrium described by Proposition 1 is
inefficient. That is, there exist feasible consumption paths that would increase its
welfare measure Wτ. However, owing to the time inconsistency of committees' preferences,
these paths are not implementable. Any future committee at time τ′ > τ can increase its
welfare measure by deviating from the time τ committee's optimal plan. The time τ
committee knows this, anticipates the behaviour of all future committees, and reacts
optimally to this knowledge. Since all committees behave this way, the resulting
equilibrium is inefficient, but fully rational. Thus, although each committee's welfare
measure aggregates its members' preferences efficiently, the interactions between
successive committees lead to an inefficient intertemporal equilibrium.

<hs>  Voting</hs>
  ~~~~~~

The fact that utilitarian committees choose inefficient consumption plans in equilibrium
suggests that alternative methods for aggregating member's opinions could improve on
utilitarian preference aggregation. The most natural alternative to consider is
majoritarian voting. Aside from being widely deployed in practice, majority rule has been
shown to satisfy desirable properties of preference aggregation over a larger domain of
preferences than any other ordinal social choice rule (Dasgupta and Maskin, 2008, see also
May, 1952). Yet as Sen (2017, p. xxvii) observes, ‘when it comes to welfare economics,
majority decision is not a particularly just, or even plausible, way of judging
alternatives'. Sen is referring here to the fact that decisions implemented by majority
rule will generally not promote more comprehensive measures of social welfare. Indeed,
while majoritarian ballots have been a staple of the positive theory of public choice for
decades (e.g. Black, 1948; Downs, 1957; Meltzer and Richard, 1981), they are seldom
invoked as a means to pursue normative social objectives. We will show below however that
our model provides one instance in which majoritarian voting may be desirable according to
such a normative objective. Voting on consumption may lead all committees to achieve
higher levels of utilitarian welfare Wτ than attempting to maximize Wτ directly. Suppose
that consumption Cτ is to be decided by ballot in each period. In each period τ, each
committee member may nominate a single value of Cτ. All members vote over each pair of
nominated consumption values, and the value that gets a majority of votes wins each
pairwise contest. A Condorcet winner (if it exists) is a value of Cτ that wins every
pairwise contest. If there is a Condorcet winner, it is implemented. Since the current
choice of Cτ influences the consumption choices that will be made in future ballots,
committee members must anticipate the outcomes of those ballots when forming their
preferences over current consumption Cτ. We assume that members are rational, and thus
anticipate the outcomes of all future ballots when forming their preferences over Cτ.7 The
following proposition characterizes the equilibrium consumption path that emerges from
this sequence of ballots: Committee members at time τ who anticipate the outcome of votes
over public consumption in future periods have single-peaked preferences over current
consumption Cτ. Thus, the equilibrium of a majoritarian voting model with ballots in every
period is the optimal consumption plan of the median member. This result may seem to be in
conflict with the analysis of voting over consumption streams in Jackson and Yariv (2015).
They show that voting over consumption streams in unrestricted domains is generically
intransitive, and thus voting equilibria cannot be represented by the preferences of a
single individual such as the median agent. Their analysis assumes however that votes are
once off, whereas in our result ballots are repeated, so that in each period members are
only voting over a single, unconstrained, value of consumption. The repeated ballot
formulation is compelling, as it does not require the somewhat far-fetched assumption that
members believe that a consumption plan that is decided on today will automatically be
implemented by all future committees.

<hs>  Utilitarian aggregation vs. voting</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We are now in a position to compare the equilibrium implemented by utilitarian committees
to that implemented by committees that vote on consumption. Our first result provides a
lower bound on the number of committee members who prefer the voting equilibrium to the
equilibrium implemented by utilitarian committees: In every period, a majority of members
prefer the voting equilibrium to the equilibrium implemented by any utilitarian committee.
This result is independent of any assumptions about utilitarian committees' aggregation
weights. Thus, regardless of how such committees aggregate preferences, a majority of
members will think that voting on discount rates will lead to superior outcomes than
attempting to maximize Wτ directly. Next, we take this observation further by
investigating when voting dominates direct maximization of Wτ, according to the welfare
measure Wτ itself. In addition, denote the median committee member's discount rate by δm.
Assume that η ≥ 1. Then, The first part of the proposition shows that utilitarian
committees inherit the single-peakedness of their members' preferences on the space of
single-agent optimal paths. Although it is not true in general that a weighted average of
single-peaked preferences is single-peaked, this does hold for our model. Since
utilitarian committees' preferences over discount rates are single-peaked, it is useful to
know something about where their ‘bliss point’ discount rate lies. The second part of the
proposition shows that it always lies below the discount rate that replicates the
utilitarian equilibrium. This is intuitive, as the commitment problem utilitarian
committees face always causes them to be more short-termist than they would like to be.
The final part of the proposition combines parts 1 and 2 to provide a simple sufficient
(but not necessary) condition for voting to dominate the utilitarian equilibrium. This
condition applies regardless of the model's primitives, although checking whether Eq. (14)
is satisfied requires us to specify these primitives.

        Logarithmic utility function (i.e., η = 1)

        When η=1 the equilibrium condition for the dynamic game between utilitarian
        committees has a closed form solution (Eq. (10)), and members' opinions on welfare
        in the voting and utilitarian equilibria can be computed analytically. This allows
        us to obtain a sharp result on when voting will dominate utilitarian aggregation,
        according to a utilitarian objective function. Assume η = 1. Then voting gives
        rise to higher utilitarian welfare than direct attempts to optimize Wτ if and only
        if Fig. 1 plots the set of three element distributions that satisfy these
        conditions. The figure shows that Eq. (18a) is almost equivalent to requiring that
        the distribution of discount rates have positive non-parametric skewness, i.e. ⟨δ⟩
        > δm. The vast majority of distributions that satisfy Eq. (18a) have this
        property. However, there is a small set of distributions that satisfy Eq. (18a),
        but have ⟨δ⟩ < δm, indicated by region C in the figure. The figure also
        demonstrates that the condition (17a), satisfied in region B of the figure, is
        sufficient but by no means necessary for voting to dominate the equilibrium
        implemented by utilitarian committees. The approximate positive skewness condition
        needed for voting to dominate the utilitarian equilibrium in this example conforms
        to intuition. When the distribution of discount rates exhibits positive skewness
        there is a long tail of large discount rates above the median. These discount
        rates have a disproportionate influence on the equilibrium implemented by
        utilitarian committees. If a committee with aggregation weights (Eq. (16)) could
        control consumption for all time, it would choose a consumption path that
        satisfies impatient members in the short run, and patient members in the long run.
        Short-run consumption choices are thus always dominated by the concerns of
        impatient committee members. However, because the current committee cannot bind
        the hands of future committees, its consumption choice is in effect always short-
        termist, and thus impatient members' preferences exert a large influence on it.
        Since this is true for every committee, the equilibrium consumption path
        implemented by a sequence of utilitarian committees will be biased towards more
        impatient members. This is reflected in the fact that the equilibrium implemented
        in this case is observationally equivalent to the optimal plan of an agent with
        discount rate ⟨δ⟩. It is well known that the arithmetic mean is sensitive to the
        large ‘outliers' that exist when the distribution of δ is positively skewed. By
        contrast, the voting equilibrium is robust to the presence of these large
        outliers, and is thus not subject to the same distortions.

        More general iso-elastic utility functions (i.e., η > 1)

        When η > 1, the equilibrium condition (10) must be solved numerically. In order to
        do this, we must specify the distribution of opinions on the PRSTP. We will use a
        distribution of discount rate prescriptions elicited from economists who are
        experts in public project evaluation (Drupp et al., forthcoming). This
        distribution is illustrated in Fig. 2. In addition, throughout this subsection we
        assume that the utilitarian committee aggregates preferences using the welfare
        weights in Eq. (16), i.e. yi ∝ δi. Given these assumptions, standard numerical
        methods can be used to solve Eq. (10), and the welfare committees achieve under
        voting and utilitarian aggregation can be computed as functions of the parameters
        r,η. The results in Fig. 3(a) and (b) are difficult to explain intuitively, as we
        need to know how both equilibria, and the way they are evaluated, vary with r and
        η. Since we do not have an analytic expression for the consumption path
        implemented by utilitarian committees, this is a difficult task. Ultimately,
        welfare comparisons for η > 1 depend on the empirical details, including the
        distribution of discount rates. Nevertheless, Fig. 3(b) shows that in our
        calibration of the model there is a large region of empirically plausible
        parameter values where voting yields better utilitarian outcomes than the
        equilibrium utilitarian committees would choose for themselves.

<h>CONCLUSIONS</h>
-----------

In this paper, we have contrasted two of the most natural preference aggregation methods
that committees of decision-makers might employ when attempting to resolve normative
disagreements about social time preferences: utilitarianism, and majoritarian voting.
While in normal circumstances voting cannot hope to compete with direct optimization of a
utilitarian objective function, the time inconsistency of utilitarian committees'
collective preferences leads them to implement inefficient consumption plans. We have
shown that this can cause voting to yield better outcomes, according to utilitarian
committees' own objectives. Indeed, our simple empirical analysis using an elicited
distribution of expert opinions on the pure rate of social time preference suggests that
this occurs in empirically plausible cases. An interesting feature of model is that,
regardless of how utilitarian committees aggregate preferences, a majority of decision-
makers will believe society to be better off if committees vote on consumption than if
they attempt to maximize their utilitarian welfare measure directly. There is thus a sense
in which majoritarian voting is ‘self-stable’ with respect to utilitarian aggregation. The
concept of self-stability was introduced by Barbera and Jackson (2004) in the context of
their study of constitutions. A voting rule X for ‘ordinary business' (e.g. deciding on
discount rates) is self-stable relative to an alternative voting rule Y if when society
votes on whether to change the voting rule from X to Y, and uses the rule X to adjudicate
this vote, it chooses to stick to X.9 With a little modification, we can adapt this
concept to our analysis. If majority voting is also used to decide whether to use
majoritarian voting or utilitarianism to aggregate members' preferences, voting will
always be selected. By contrast, if the choice between the two aggregation methods is made
based on comparisons of the equilibrium utilitarian welfare they achieve, we have shown
that there are plausible circumstances under which voting dominates utilitarianism. In
these circumstances, majoritarian voting is self-stable, but maximizing utilitarian
objectives is not. It is clear from the expression above that the PRSTP δ is a critical
input to rt — small changes in its value can have a very large impact on the evaluation of
public projects with long-term consequences (see e.g. Heal and Millner, 2014). In
practice, governments revise their choices of the social discount at semi-regular
intervals (Gollier and Hammitt, 2014), and debates about the appropriate value of the
PRSTP are invariably part of this process. While the processes that are used to resolve
ethical disagreements about the PRSTP are currently ad hoc and rather opaque, our work
takes a more systematic approach to the aggregation of viewpoints on social impatience.
Our conclusion is that voting on the PRSTP is likely to have advantages over utilitarian
aggregation in practice. Our simple empirical analysis suggests that a consensus value of
δ ≈ 0.5%/yr could emerge from such a vote. This value is considerably smaller than that
advocated by e.g. Nordhaus (2008) in his analysis of climate change policy (he favours
1.5%/yr), but larger than the value of zero advocated by e.g. Stern (2007) and Gollier
(2012) based on their personal ethical views. The main limitation of our analysis is the
assumption that committee members share a common utility function. This assumption is made
only for technical reasons. It is possible to extend our results on the voting equilibrium
to the case where committee members favour different iso-elastic utility functions.10
However, solving for the equilibrium of the dynamic game between utilitarian committees
becomes difficult in this case, as the committee's preferences are no longer iso-elastic,
and thus the limit equilibrium is generically non-linear. Similar tractability issues
arise for more general (i.e. non-linear) production functions. Nevertheless, the
qualitative finding that voting may dominate direct utilitarian aggregation will continue
to hold even in these substantially more complex cases.


<h>REFERENCES</h>
----------

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<ART>Discouragement effect and intermediate prizes in multi-stage contests: Evidence from Davis Cup
================================================================================

Authors: Hamzah Iqbal, Alex Krumer
DOI: 10.1016/j.euroecorev.2019.06.001
Year: 2019  |  Pages: 364-381
ASJC codes: 2002, 2003
Keywords: Collective decision-making, Discouragement, Multi-stage contests, Tennis

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

The discouragement effect of being the lagging player in multi-stage contests is a well-documented phenomenon. In this study, we utilize data from 2447 Davis Cup matches in team tennis tournaments to test the effect of being behind or ahead on individuals’ performance with and without intermediate prizes. Using several different strategies to disentangle the effect of being ahead in the interim score from the effect of selection, we find the usual discouragement effect. However, the discouragement effect disappears after the introduction of intermediate prizes in the form of ranking points. The lagging favorite had close to a 20-percentage point greater probability of winning compared to matches without such a prize. We show that this result is not driven by the selection of better players into tournaments with intermediate prizes. As predicted by previous theoretical studies, our empirical findings suggest that intermediate prizes may mitigate or even eliminate the ahead–behind effects that arise in multi-stage contests.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

One of the fundamental relationships in the economic environment in general and in
tournament settings in particular is the relationship between incentives and performance.
It has been well-documented that higher stakes enhance the performance of higher ability
agents (Rosen, 1986; Ehrenberg and Bognanno, 1990; Lazear, 2000; González-Díaz et al.,
2012; Jetter and Walker, 2015). Another important feature that is frequently found in
multi-stage tournaments is ahead–behind asymmetry, where one contestant has an advantage
over the other by having a better previous performance. Such situations may occur in R&D
contests (Harris and Vickers, 1987), political campaigns (Klumpp and Polborn, 2006), job
promotions (Tsoulouhas et al., 2007), and sports competitions (Malueg and Yates, 2010).
This ahead–behind asymmetry creates a discouragement effect, according to which a lagging
player has fewer incentives to exert costly efforts and therefore is more likely to lose
in the following stages.1 There is also a psychological explanation according to which
ahead–behind asymmetry creates additional psychological pressure on the lagging player,
which in turn harms his/her performance and reduces his/her probability of winning
(Apesteguia and Palacios- Huerta, 2010; Genakos and Pagliero, 2012; Palacios-Huerta, 2014;
Genakos et al., 2015; González-Díaz and Palacios-Huerta, 2016). The combination between
incentives and ahead–behind asymmetry was studied theoretically by Konrad and Kovenock
(2009). They showed that intermediate prizes in multi-stage contests might mitigate the
discouragement effect on the lagging player. The intuition behind their result is that a
lagging player has more incentive to exert effort in every stage, because the player is
competing for an additional prize that can be achieved regardless of the interim gap
between the players. In a more recent theoretical study, Fu et al. (2015) investigated
multi-stage contests, where individuals from two teams compete in pairwise battles. In
their model, a team that wins the majority of battles receives a team prize and,
additionally, the winner of each pairwise battle receives an individual prize. The authors
established the so-called strategic neutrality, according to which the existence of an
individual prize eliminates any ahead–behind effect and the probability of winning in
every single battle depends only on the players’ innate ability, not on the outcome of the
past battles. In general, studying the performance of individuals within a team framework
is an important economic and managerial task because in most professions, teamwork is the
rule rather than the exception. For example, a recent report by the European Foundation
for the Improvement of Living and Working Conditions (Eurofound, 2014) holds that, in 31
out of 37 sectors, teamwork prevails in over 50% of activities. However, studying the
performance of individuals in non-experimental contests between teams is not a trivial
task because reality rarely creates situations that allow a clear view of the contribution
of individuals to a team's output. Therefore, the empirical literature is scarce and based
mostly on laboratory experiments.2 A notable exception is the orange grove field
experiment conducted by Erev et al. (1993), where the authors found that inter-group
competition produced a significantly higher output than in the case where subjects were
paid according to their individual output or when they received an equal share of the
group's total output. In this paper, we are motivated by the scant empirical evidence from
non-experimental settings on the performance of individuals within a team framework, in
general, and on the interactive role of incentives and ahead–behind asymmetry in
particular. Therefore, the aim of this paper is to test empirically the effect of
ahead–behind asymmetry on individuals’ performance in multi-stage contests between teams
with and without intermediate prizes using data from tournaments among highly competitive
and extensively trained professionals. To that end, we utilized data from tennis matches
in the Davis Cup tournament, which is the premier international team event in men's
tennis. Each tie between two nations consists of five separate pairwise matches. A team
that wins three matches wins the tie.3 Therefore, by construction, before the second and
fourth matches of the tie, one of the teams should have more wins than the other. This
structure allows us to study the performance of the lagging/leading players.4 More
importantly, a change of tournament rules in 2009 makes it feasible to study the effect of
intermediate prizes. According to this change, between 2009 and 2015, a player who won a
single match in the World Group received individual ranking points. In other years and
groups, there were no individual prizes for winning a single match. Utilizing data from
professional sports where contestants have strong incentives to win has several
advantages. First, it eliminates any possible skepticism about applying behavioral
insights obtained in a laboratory to non-experimental settings (Hart, 2005). Second,
sports contests involve high-stake decisions that are familiar to the agents. Third, it
provides a unique opportunity to observe and measure performance as a function of
variables such as heterogeneity in abilities and prizes. Fourth, at each point in time,
the contestants have complete information about the interim score and the status of the
tournament. Indeed, as Kahn (2000) argues, sports data are very unique in that they embody
a large amount of detailed information that can be used for research purposes.5 Since
being ahead or behind in the interim score is not determined randomly (for example, home
teams or stronger tennis nations have a greater probability of being ahead in the interim
score), we use several different strategies to disentangle the effect of leading/lagging
from the effect of selection. First, we estimate the average treatment effect of
leading/lagging by using the distance-weighted radius matching approach with bias
adjustments suggested by Lechner et al. (2011) that has been shown to have superior finite
sample properties relative to a broad range of propensity score-based estimators (Huber et
al., 2013). We also use Oster's (2019) recently proposed bias-adjusted estimator. Based on
the analysis of 2447 matches from 966 international ties, we find a significant
ahead–behind influence on players’ performance, which is mostly pronounced in match 4,
which is likely because of the unique schedule of the tie. More specifically, we find that
the favorite (higher ranked player) has about a 10-percentage point greater probability of
winning a match if his team is leading. However, the main contribution of this paper is
that we have a unique opportunity to study the performance of players in tournaments with
and without intermediate prizes. As already mentioned, in 2009, the Association of Tennis
Professionals (ATP) decided to assign ranking points to the winner of a single match in
the Davis Cup. These points are taken into account in determining the World Ranking list.
Based on this list, players enter the most prestigious tournaments with the possibility of
earning large monetary prizes.6 Investigating matches in the World Group with and without
intermediate prizes (ranking points, in our case), we find that before the decision to
assign ranking points for winning a single match, a favorite from the leading team was
more likely to win in match 4 than the favorite from the lagging team. However, from 2009
to 2015, the gap between the probabilities of the lagging and leading favorites’ winning
disappeared. We also show that this result is not driven by the selection of better
players into the tournament after the change. Our findings suggest that the introduction
of intermediate prizes mitigates and may even eliminates the ahead–behind effects that
arise in multi-stage contests. The remainder of the paper is organized as follows. Section
2 describes the Davis Cup setting. The data and descriptive results are detailed in
Section 3. Section 4 describes the estimation strategy. In Section 5 we present the
evidence about the ahead–behind effect. Section 6 reports the effect of intermediate
prize. Finally, in Section 7 we offer concluding remarks.

<h>DESCRIPTION OF THE DAVIS CUP</h>
----------------------------

The Davis Cup is an international men's tennis team competition played annually between
teams from participating countries. The tournament is structured into five hierarchical
levels: World Group, Group 1, Group 2, Group 3, and Group 4. The World Group is the top
competition level, comprised of 16 participating nations. Nations that are not part of the
World Group compete in one of the lower four groups. Teams in World Group, Group 1 and
Group 2 compete in elimination tournaments according to which the winning team advances to
the next round and the losing team is eliminated. Groups 3 and 4 use a round-robin
structure according to which teams play against each other in pairwise ties.7 A tie
signifies a competition round between two competing countries. In the World Group, for
example, the 16 nations play eight pairwise ties in the first round (the round of Last
16). The eight winners of this round compete in four Quarterfinal ties. The four winners
play two Semifinal ties. Finally, the two winners play the Final tie. Teams from World
Group to Group 2 that lose in the first round face the possibility of being relegated to a
lower group for next year's tournament. Promotion or relegation in the World Group is
decided in Play-off rounds played between losers of the first round in the World Group and
winners of Group 1. To be promoted from Group 2 to Group 1, a team needs to win in three
different rounds. A team that loses in three different rounds in Groups 1 and 2 is
relegated to a lower group. Each tie in the World Group, Group 1 and Group 2 consists of
five rubbers (matches), namely, four singles matches and one doubles match. Each team
consists of several players who are seeded according to their individual World Rankings.
On the first day of each tie, two matches are played between the first seeded player of
one team and the second seeded of another team. The schedule of the first day is
determined randomly. The doubles match is always scheduled as match number 3, which takes
place on the second day of the tie. On the third day, the two top seeded players from each
team always compete against each other in match 4 and two second seeded players from each
team always compete in match 5. The first team that wins three rubbers wins the tie and
progresses to the next round to play a tie against another team. If the tie has not
already been decided in favor of one team (no team won three rubbers), then the remaining
rubbers are termed live rubbers, which are played in the form of best-of-five sets.
Additionally, all dead rubbers are played in the form of best-of-three sets.8 Finally,
between 2009 and 2015 a player who won a single rubber in the World Group received ranking
points as long as the rubber was defined as a live rubber. In other years and groups there
were no individual prizes for winning a single rubber.

<hs>  Data</hs>
  ~~~~

As already stated, since there is a difference between the round-robin and elimination
formats, our dataset consists of Davis Cup matches in the World Group, Group 1 and Group 2
that use the latter format. In addition, we consider only matches between individuals and
do not use matches between doubles because, in most cases, players do not specialize in
doubles and play these types of matches only occasionally. The data were collected from
several websites (see Appendix A for a list of all sources). All Davis Cup matches played
between 2003 and 2015 are present in the datasets. For every match, information is
available regarding the names of the players, their previous head-to-head victories and
losses against the opponent, and each player's 52-week ranking prior to the beginning of
each match. The ranking is used as a measure of the players’ abilities and is calculated
and updated weekly by taking into account all of the player's results in professional
tournaments over the previous 52 weeks. Apart from individual level data, information on
the location, group type, year, and tournament round for each tie is also available. In
all, the dataset consists of 4206 Davis Cup matches. However, we consider only live
rubbers (i.e., matches that are still crucial in deciding which team wins the tie) because
dead rubbers are in the form of best-of-three sets and usually substitute players compete
in these matches. Therefore, 1198 dead rubber matches were eliminated. In addition,
another 561 matches lacked information regarding the current ranking of one of the
players, or were not played to completion, and therefore were eliminated as well.9
Dropping all of these matches leaves 966 Davis Cup ties, consisting of 2447 matches.

<hs>  Variables</hs>
  ~~~~~~~~~

For each match, we first define the higher ranked player as the favorite and the lower
ranked one as the underdog. Then, we estimate the probability that the favorite will win
the match. Accordingly, we assign the dependent variable a value of one if the favorite
player won and zero otherwise. It is important to note that a favorite is lagging if the
interim score of the tie before the respective match is 0:1 or 1:2 in favor of the
opponent's team. A favorite is leading if the interim score of the tie before the
respective match is 1:0 or 2:1 in favor of his team. Therefore, to estimate the effect of
being ahead/behind in the score, we coded a dummy variable that equals one if the favorite
is lagging before the respective match and zero otherwise. Similarly, we coded a dummy
variable that equals one if the favorite is leading before the respective match and zero
otherwise. We also control for the home advantage, which was found to play a significant
role in professional tennis (Koning, 2011). Thus, the variable indicating that the
favorite has a home advantage receives the value of one if the favorite competes at home
and zero otherwise. In addition, we include dummies for each round and type of group
categories. Finally, since starting from 2009 a single win in a live rubber of the World
Group guaranteed ranking points, we coded a dummy variable that equals one if the match
was in the World Group after 2009 and zero otherwise. The descriptive statistics of our
dataset are presented in Table 1. It indicates that, on average, the favorite wins in
68.1% of cases if his team is lagging. It also shows that if the favorite's team is
leading, his probability of winning is 80.4%. Using a 95% confidence interval, Fig. 1
shows that the favorite's share of wins when his team is leading (1:0 or 2:1) is
significantly higher than when the interim score is a draw (0:0 or 2:2) or when the
favorite's team is lagging (0:1 or 1:2). However, Table 1 also indicates that if the
favorite is leading, he also has more of a home advantage, better head-to head
performance, and a lower ranking index, which is associated with greater relative ability.
Thus, in order to obtain the causal effect of being ahead/behind, we will use several
estimation strategies that control for selection into treatment (leading/lagging). We
discuss these strategies in the following section.

<h>ESTIMATION STRATEGY</h>
-------------------

Studying whether being ahead or behind before a Davis Cup match gives an advantage to the
favorite is a challenging task. A naïve approach of correlating a dummy variable for
leading/lagging with the probability of winning a match will yield biased and inconsistent
estimates because the status of being ahead or behind is not determined at random. Rather,
as mentioned earlier, being ahead is a function of features specific to tennis such as
home advantage, previous head-to-head meetings, and the difference in abilities between
the other members of the teams. Furthermore, isolating an exogenous source of being
ahead/behind in the score by using an instrumental variable approach seems unfeasible
because any factor that might be associated with being ahead/behind is also likely to
affect the probability of winning the match. In the absence of a valid instrument, we will
use several alternative strategies to control for the endogeneity of leading or lagging in
Davis Cup matches.

<hs>  Radius matching estimator</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~

Our main analysis is based on the radius-matching-on-the-propensity score estimator with
bias adjustment (Lechner et al., 2011). Not only was it found to be very competitive among
a range of propensity score related estimators, but also a later paper by Huber et al.
(2013) actually demonstrated its superior finite sample and robustness properties in a
large-scale empirical Monte Carlo study.10 The main idea of this estimator is to compare
treated and non-treated observations within a specific radius. The first step consists of
distance-weighted radius matching on the propensity score. In contrast to standard
matching algorithms where controls within the radius obtain the same weight independent of
their location, in the radius matching approach, controls within the radius are weighted
proportionally to the inverse of their distance to the respective treated observations to
which they are matched. The second step uses the weights obtained from this matching
process in a weighted linear or non-linear regression in order to remove biases due to
mismatches. Because this approach uses all comparison observations within a predefined
distance around the propensity score, it allows for greater precision than fixed nearest
neighbor matching in regions in which many similar comparison observations are available.

<hs>  Radius matching analysis</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~

First, we conducted the analysis for the full dataset. As already discussed, there is a
selection into being ahead/behind. Although the purpose of the propensity score estimation
is only a technical one, namely, to allow the easy purging of the results from the effects
of selection, it is nevertheless interesting to see which variables drive selection. In
Table 2 we report the results for the propensity score estimation. We use two different
specifications. In the first, we control for differences in rankings, previous head-to-
head results and home advantage. In the second specification, we also control for specific
features of the ties, such as the round of the tournament, the group, the year and whether
the match is a World Group match before or after 2009. We can see that many variables are
associated with being ahead/behind. This finding is not surprising because we would expect
home players to be more likely to win and players from stronger countries have, on
average, better teammates. In Columns 1 and 2 of Table 3 we present the results for the
radius-matching estimator where Panel A and Panel B report the average effects for lagging
and leading, respectively. The clustered standard errors at the tie level are presented in
parentheses. The results show that the effect of lagging is negative and significant. It
reduces the favorite's probability of winning by about 5 percentage points. The effect of
being ahead on the favorite's probability of winning is between 3.7 and 5.4 percentage
points and also significant. This finding is in line with the ahead–behind asymmetry that
has been found in soccer (Apesteguia and Palacios-Huerta, 2010; Palacios-Huerta, 2014) and
chess (González-Díaz and Palacios-Huerta, 2016). It is important to note that our results
do not contradict those of Berger and Pope (2011) who found that being slightly behind
(one point) at half-time has a positive effect on the probability of winning in
basketball. However, being far behind is less likely to have a positive effect. Since in
the Davis Cup there are only five matches, being one match behind is a much more
significant lag than being one point behind in basketball, where teams score about 100
points per match. Therefore, we interpret lagging by one match in the Davis Cup as being
further rather than slightly behind.

<hs>  Oster's bias-adjusted treatment effect</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

It is important to note that the radius-matching-on-the-propensity score estimator is very
flexible, without strict assumptions about the functional form. Nevertheless, as a
robustness check we also use Oster's bias-adjusted estimator, which relies on a strict
functional form, making it much less flexible than the semi-parametric matching estimator.
In order to conduct the treatment effect of leading/lagging, in Columns 3 and 4 of Table
3, we present the results of the linear probability model (LPM) without and with the full
set of controls respectively where standard errors clustered at the tie level appear in
parentheses. Not surprisingly, we can see that the size of the coefficients of Favorite is
lagging and Favorite is leading are much higher in the uncontrolled specification
presented in Column 3 than in the specification with the full set of controls presented in
Column 4. In Column 5 we present the bias-adjusted treatment effect of lagging/leading.
The standard errors obtained from the bootstrap are presented in parentheses. The results
show that the estimated causal effect is closer to zero, but still significant. When a
favorite is lagging, he is 3.7 percentage points less likely to win with a significance
level of 5.3%. The positive effect of being ahead on the favorite's probability of winning
is 3.6 percentage points with a significance level of 3.9%.11

<hs>  Ahead–behind asymmetry in matches 2 and 4</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In this subsection our aim is to investigate only matches where the score is asymmetric,
namely matches 2 and 4, where by construction, one team is leading and the other is
lagging before the beginning of the match. Fig. 2(a) and (b) shows that on average there
is a much larger gap between the share of wins if a favorite is leading in match 4
compared to match 2. Our empirical analysis presented in Table 4 demonstrates that being
ahead has a significant and positive effect on the probability of winning in match 4. We
find no significant effect of being ahead in match 2.12 This result is in line with
several explanations. First, as already mentioned, matches 1 and 2 are played between the
first seeded player of one team and the second seeded of another team, whereas match 4
involves the two top seeded players from each team. Thus, it is intuitive that a lagging
favorite competes against a weaker opponent in match 2 compared to match 4. Therefore, the
discouragement effect is less likely to appear in match 2, because being down 1:0 in a
Davis Cup meeting is almost an expected event. However, it is possible that the favorite
player loses in the first match, which can have a different effect on the performance of
the players in the second match. Therefore, in Appendix D we present the results of match
2 for cases in which a favorite won and lost in the first match. We find that if a
favorite won in the first match, then being ahead in the second match has a positive
effect on the probability of winning. However, this effect is not significant at
conventional levels. We also observe a negative coefficient if the favorite lost in the
first match. Nevertheless, the result is far from being significant. There are some
additional explanations for the difference in results between matches 2 and 4. For
example, it is possible that a lagging player has much more to lose in terms of a team
prize in match 4 compared to match 2 because if a lagging player loses in match 4, his
team loses the entire tie. Therefore, such a situation may provoke choking under pressure
of the lagging player and, as a result, harm his performance and reduce the likelihood of
his winning.13 Finally, it is also possible that the leading player values his win more
than the lagging player in match 4 compared to match 2, which may also result in a
difference in the probabilities of winning. This difference in valuations between the
matches may be driven by simple egocentric motives. For example, the winner of the match
that determines the tie gets more glory. Although we cannot observe all of the possible
prizes the players receive from winning a single match, in the next sub-section we use a
unique opportunity to study the effect of the ahead–behind asymmetry in settings with and
without intermediate prizes.

<hs>  Introduction of ranking points in the World Group in 2009</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In this section, we take advantage of the change in the rules introduced by the ATP. Up to
2009, players did not receive any ranking points for a single win. However, between 2009
and 2015, the winner of a live rubber of the World Group received ranking points. These
points are taken into account in determining the World Ranking list. This list is very
important because it determines the entries to the most important tournaments with the
largest monetary rewards. In addition, players with a higher number of points may benefit
from a better draw, because in the first rounds they play against weaker players. To put
this decision into perspective, a win in a main tournament of the Davis Cup was worth
40–75 ranking points, depending on the round. This means that two wins in Davis Cup
matches were worth more than two wins in the first two rounds of Grand Slam tournaments
(55 points), which are the most prestigious tennis tournaments.14

<hs>  Theoretical framework</hs>
  ~~~~~~~~~~~~~~~~~~~~~

As discussed, theoretically, the intermediate prizes (ranking points) play a very
important role in multi-stage contests. According to Konrad and Kovenock (2009), the
introduction of positive intermediate prizes may increase the lagging player's probability
of winning. Moreover, according to Fu et al. (2015), if there is an intermediate prize,
which is common to both players, the interim score of a tie has no effect on the players’
probability of winning in a single rubber. This probability depends only on the players’
innate abilities. In Section 2 we noted that the last two matches involve the top seeded
players from each team in match 4, and the two second seeded players from each team in
match 5. In contrast, the first two matches always involve the first seeded player of one
team and the second seeded of another team. Intuitively, match 4 is more symmetric than
match 2. Indeed, in our dataset, the mean DiffRank value in match 2 equals −1.79, which is
significantly lower than the mean DiffRank value in match 4, which equals −1.59 (two-
sample mean comparison p-val=0.009). This result illustrates that match 4 is significantly
more symmetric than match 2. Therefore, in our model between two symmetric players, we
will present only the case of the last two matches, because they bear a closer resemblance
to the empirical settings.

<hs>  Empirical evidence</hs>
  ~~~~~~~~~~~~~~~~~~

Although our empirical settings do not fully resemble our theoretical model or the
theoretical settings of Fu et al. (2015) and Konrad and Kovenock (2009), we still wish to
test whether starting from 2009, the probability of winning is affected by the state of
the contest (whether a player is leading or lagging). Based on the World Group ties, Fig.
4(a) shows that the gap between the probabilities of winning when one is leading in match
4 compared to being behind was, on average, 28 percentage points before the change in the
rules in 2009.15 However, as Fig. 4(b) illustrates, this gap declined dramatically to only
8 percentage points after 2009.

     <hss>Selection issue</hss>

        One possible concern, however, is that the introduction of the ranking points may
        attract better players. Therefore, the greater probability of the lagging
        favorite's winning might be attributed to selection rather than to intermediate
        prizes. To obviate this concern and show that the players’ rankings are not
        differently distributed before and after 2009, we use the following two-step
        procedure. First, we partitioned the data into two parts, where one set contains
        the World Groups’ match 4 before 2009 and the other the World Groups’ match 4
        after 2009. In Table 5 we report the average value of the log2 of the ranking of
        the favorite, the underdog and the differences between them on the match level,
        separately for each period. In parentheses we present their standard deviations.
        Column 1 refers to the matches before 2009, while Column 2 refers to the matches
        after 2009. We can see that the log2 of the players’ rankings is even somewhat
        higher after 2009, implying the rankings of those with less ability. Then, we run
        a set of univariate regressions of each of the variables presented in Table 5 on a
        dummy variable indicating whether the specific observation was before 2009. The
        coefficient of this dummy variable and its standard error are presented in Column
        3. The results show that none of these players’ characteristics differ
        significantly between the two periods. This finding indicates that the players’
        log2 of rankings and their differences do not differ before and after 2009.
        Therefore, we can conclude that selection into the sample is not a concern.

     <hss>Radius matching analysis</hss>

        In Table 6, we present the effects of leading in match 4 on the probability of the
        favorite player's winning before and after 2009. The radius-matching estimator
        presented in Column 1 implies that there is a significant and positive effect of
        being ahead before 2009, which is much smaller and not significant after 2009.
        Finally, we test whether the intermediate prizes increase the probability of the
        lagging player's winning, as indicated in Fig. 4(a) and (b). In Table 7, we
        compare the probabilities of the lagging favorites’ winning in match 4 before and
        after 2009. In total, we have 45 such cases before 2009 and 43 after. The results
        of the radius-matching estimator presented in Column 1 imply that the effect of
        the intermediate prizes on the probability of the lagging favorite's winning is
        18.4 percentage points with a significance level of 6%. It is important to note
        that similar to the results presented in Table 5, in the case with the lagging
        favorite as well, none of the characteristics significantly differs between the
        two periods, before and after 2009. In fact, as Appendix F indicates, none of the
        variables has a p-value lower than 0.31. This result serves as additional evidence
        that selection into the sample is not a concern.16

     <hss>Oster's bias-adjusted treatment effect</hss>

        As previously, we use Oster's bias-adjusted estimator as a robustness check. In
        Columns 2–3 of Table 6 we present the LPM's coefficients of Favorite is leading in
        match 4 in the World Group before and after 2009, where robust standard errors
        appear in parentheses. Given the very small number of observations, the R-squared
        is very sensitive to the inclusion of any additional variable. Therefore, we
        follow Oster (2019) who also offers an adjusted procedure for evaluating the bias-
        adjusted treatment effect when some variables are considered part of the
        identification strategy and thus appear in both the controlled and uncontrolled
        regressions. The idea is to assess the amount of selection on the observables
        conditional on including these variables in the estimation. Because some of the
        variables are significant in the propensity score estimation presented in Appendix
        E, it is worthwhile assessing the amount of selection conditional on these
        variables being included in the estimation as part of our identification strategy.
        Therefore, in Columns 2 and 3 of Panel A in Table 6, which represents the matches
        before 2009, the DiffRank and Year2008 are included in both the controlled and
        uncontrolled regressions. Similarly, since DiffRank is significant in the
        propensity score estimation (Column 2 in Appendix E), in Panel B of Table 6, we
        include it in both the controlled and uncontrolled regressions (Columns 2 and 3).
        We can see that the coefficients are significant before 2009 and even somewhat
        higher when including the controls (Columns 2 and 3 of Panel A in Table 6).
        Therefore, by definition, Oster's bias-adjusted coefficient has to be even farther
        from zero, as we can see in Column 4 of Panel A in Table 6. However, the
        bootstrapping procedure in the dataset that includes 89 observations only
        increases the standard errors and the p-val to 0.125. Nevertheless, the most
        important result in this case is that Oster's bias-adjusted coefficient becomes
        even larger compared to the LPM. When testing the effect of leading after 2009, we
        can see that according to all of the estimators (Columns 2–4 of Panel B in Table
        6), the effect of leading in match 4 is much closer to zero and highly
        insignificant. Finally, in order to conduct Oster's bias-adjusted treatment effect
        of playing after 2009 on the lagging player's probability of winning, we use the
        results of the LPM with and without the full set of controls as presented in
        Columns 2 and 3 of Table 7, respectively. We can see that the effect of the
        post-2009 period is not sensitive to the inclusion of the controls. Its size is
        about 20 percentage points with a significance level of 3.6% and 4.7% in Columns 2
        and 3, respectively. Not surprisingly, Oster's bias-adjusted coefficient,
        presented in Column 4, is almost the same as in the LPM, with a significance level
        of 5.6%. Taken together, our results suggest that the introduction of incentives
        for winning a single match is likely to affect the performance of players.
        Although our empirical settings do not fully match the theoretical settings of Fu
        et al. (2015) and Konrad and Kovenock (2009), our finding that the probability of
        winning is not affected by the state of the contest when an intermediate prize is
        introduced is in line with these theoretical predictions. In general, our
        empirical results emphasize the importance of the strategic allocation of efforts
        in multi-stage contests that is well known in the theoretical literature. Although
        we cannot rule out the possibility of some other psychological effects, our
        findings suggest that the introduction of intermediate prizes may mitigate or even
        eliminate the ahead–behind effects that arise in multi-stage contests.17

<h>CONCLUSION</h>
----------

In this paper, we used tournaments among highly competitive and extensively trained
professionals to test the effect of ahead–behind asymmetry on individuals’ performance in
multi-stage contests between teams with and without intermediate prizes. As in previous
studies, we find that being ahead provides players with a greater probability of success.
However, the main contribution of this paper is that it empirically shows that
intermediate prizes eliminate the usual ahead–behind effect that may arise from
psychological as well as from strategic considerations. Our results, obtained from
contests between high-profile professionals, underscore the role of strategic motives in
individual performance. This is especially important on the team level, because teamwork
is probably the most prevalent form of economic activity. Our findings suggest that non-
monetary incentives alone, such as a team's pride, are probably not enough to maximize an
individual's output. This result may be of great importance in situations that involve a
choice between individual and social benefits. Nevertheless, it is important to note that
we did not investigate the effect of team-based incentives on individual performance.
Therefore, it will be interesting to study whether the introduction of team-based
incentives instead of individual-based incentives will also lead to improved performance.
Furthermore, individual incentives may improve the utility of other teammates of the
lagging team because such incentives do not affect the winning probabilities of leading
favorites, who are likely to win the decisive match regardless of the incentives. It is
rather the lagging favorite who benefits from additional individual rewards. In addition,
his teammates benefit from the greater probability of winning the entire contest. This may
explain why companies in difficulty are ready to pay extra salaries to high-profile
workers, who are able to stabilize the firm's cash flows or profits. However, other
workers who do not receive an additional individual reward may also benefit from the
increased stability of their workplace. Finally, it is important to note that despite the
fact that our findings are in line with the common ahead–behind effects and with previous
theoretical studies on the effect of intermediate prizes, the results of this paper were
obtained from the sport of tennis, which is mostly an individual sport. Playing in teams
in the Davis Cup is not the usual competitive format for most players. Therefore, it is
possible that our results would be different in other settings, where individuals are used
to performing in teams. It is also possible that those who are not used to large monetary
rewards would also behave differently. Therefore, we call for additional empirical
research to test the interactive effect of intermediate prizes and ahead–behind asymmetry
in various other environments.


<h>REFERENCES</h>
----------

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<ART>Discrimination in the laboratory: A meta-analysis of economics experiments
==========================================================================

Authors: Tom Lane
DOI: 10.1016/j.euroecorev.2015.11.011
Year: 2016  |  Pages: 375-402
ASJC codes: 2002, 2003
Keywords: Discrimination, Meta-analysis

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Economists are increasingly using experiments to study and measure discrimination between groups. In a meta-analysis containing 441 results from 77 studies, we find groups significantly discriminate against each other in roughly a third of cases. Discrimination varies depending upon the type of group identity being studied: it is stronger when identity is artificially induced in the laboratory than when the subject pool is divided by ethnicity or nationality, and higher still when participants are split into socially or geographically distinct groups. In gender discrimination experiments, there is significant favouritism towards the opposite gender. There is evidence for both taste-based and statistical discrimination; tastes drive the general pattern of discrimination against out-groups, but statistical beliefs are found to affect discrimination in specific instances. Relative to all other decision-making contexts, discrimination is much stronger when participants are asked to allocate payoffs between passive in-group and out-group members. Students and non-students appear to discriminate equally. We discuss possible interpretations and implications of our findings.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Meta-analysis – a commonplace technique in medical science, psychology and, to a growing
extent, economics – holds advantages over literature review in terms of objectivity and
analytical rigour. In recent years, the experimental economics literature appears to have
reached a critical mass at which researchers are finding meta-analyses useful.1 The
benefit of these works is that, by aggregating data across a large number of experiments
and exploiting natural between-study design variation, they pinpoint behavioural
regularities and the variables that modify them more precisely than could be done through
qualitative review. We run a meta-analysis on the body of studies investigating
discrimination in lab and lab-in-the-field experiments, a sub-literature which has
certainly reached the necessary critical mass for such a venture. Economists׳ interest in
discrimination has been strong ever since Becker (2010), and with the growth of
experimental economics in the last two decades, experiments have emerged as a popular
complement to survey-based econometric studies. These experiments create a controlled
environment and therefore allow much cleaner measurements of discrimination than the
analysis of naturally-occurring data, avoiding such problems as omitted variable bias and
reverse causality. Furthermore, by testing for a very fundamental and general form of
discrimination – simply, whether subjects treat others differently depending on which
group those others belong to – experimental economists can produce findings of interest
not only to their own discipline but also across the social sciences. Also, through the
use of incentives, experiments hold a key advantage over questionnaire-based measures of
discrimination, in that they elicit revealed rather than reported discrimination.
Psychologists had already been studying discrimination in the lab for decades, and
experimental economists have drawn on their knowledge, particularly regarding the minimal
group paradigm. This technique was first introduced by Tajfel et al. (1971) and has
spawned a huge body of experiments wherein group identity is artificially induced in the
laboratory. This is often done by, in a preliminary phase of an experiment, asking
subjects to state their preference for one artist over another, or to randomly draw a
colour. The experimenter then splits the subject pool into groups according to their art
preference, or the colour they have drawn, and makes it known to participants that the
division is based on these differences. Subsequent stages of such experiments involve
interaction tasks between the groups and find discrimination surprisingly (at least to the
early researchers) often. To study discrimination, experimental economists set up games
such as the dictator game, the trust game or the prisoner’s dilemma, and invite a subject
pool segregated along the lines of a particular identity-based characteristic (or else
generate this segregation with artificial groups). They make subjects aware of the group
affiliation of those they interact with, and then measure how their behaviour varies
according to whether individuals they are interacting with share their identity (are in-
group) or do not (are out-group). The number of economics experiments of this type has
grown rapidly since the turn of the century and now encompasses substantial diversity
across several dimensions. Even after omitting many papers which investigate
discrimination but do not meet our inclusion criteria devised to ensure a consistent
approach (see Section 2), we are left with a dataset consisting of 441 experimental
results (significant and null) from 77 studies – more data than most of the other
experimental economics meta-analyses have had. In order to aid the progression of this
literature, it is worth taking stock of what has been found to date, particularly as
casual inspection reveals non-uniformity in the results; the strength of discrimination
found against out-groups varies considerably, and some experiments even find
discrimination in the opposite direction, i.e. against the in-group. The aim of this meta-
analysis is both to yield broad insights on discrimination and to inform the designers of
future experiments testing for it. We first investigate the average strength of
discrimination across the literature. We then inquire how it tends to vary according to
specific experimental characteristics. In particular, we are interested in whether the
strength of discrimination depends on the type of identity being investigated. Comparing
the level of discrimination between artificial (i.e. minimal) groups and various types of
natural groups (such as those based on ethnicity, nationality, religion, gender and
social/geographical affiliation) is particularly interesting. One might expect ‘minimal’
groups to yield minimal levels of discrimination. However, it is also conceivable that
artificial identity inducement confers an experimenter demand effect in favour of
discrimination, or that the experimental priming of sensitive natural identities reduces
subjects’ desire to discriminate owing to a preference not to engage in socially
unacceptable behaviour. Evidence for these possibilities, in the form of relatively strong
discrimination in artificial group experiments, could have implications for the external
validity of certain experiments. A further interesting question is whether the strength of
discrimination varies according to the type of decision subjects are asked to make. This
has implications in terms of the real-world circumstances in which discrimination can be
most expected to appear and for the generalisability of findings. We further ask whether
experiments with students reveal greater or lesser discrimination than those with non-
students. This is also important for the external validity of findings, and is a question
worth pursuing as some studies (e.g. Bellemare and Kröger, 2007; Anderson et al., 2013)
have found students are not entirely representative of wider populations in economics
experiments. This meta-analysis also aims to shed light on the motivations behind
discrimination. Some experiments have been designed specifically to distinguish between
taste-based discrimination and statistical discrimination – the two models that continue
to dominate the theoretical literature in economics. The taste-based model, proposed by
Becker (2010), entails individuals gaining direct utility from the act of discriminating
against out-groups. Meanwhile, according to theories of statistical discrimination –
beginning with Arrow (1972) – individuals aim to maximise their own payoffs given their
beliefs and expectations about others׳ characteristics and behaviour, and discrimination
occurs when those beliefs and expectations vary depending on the group to which the others
belong. Understanding the relative importance of these two motivations will improve the
focus of future research and the design of policies aimed at combating discrimination.
Finally, we include a subsection on experiments investigating gender discrimination.
Gender is unique amongst the identity types in having the same two groups in each
experiment. It is therefore simple to make a clean comparison between male-to-female
discrimination and female-to-male discrimination. In summary, the meta-analysis presented
below aims to address the following questions: (1) What is the general pattern of
discrimination across the literature? (2) How does the level of discrimination vary
according to the type of identity groups are based upon? (3) How does the level of
discrimination depend upon the decision-making context? (4) Do students discriminate any
more or less than non-students? (5) Does the experimental literature provide more support
for taste-based or statistical theories of discrimination? (6) In gender experiments, how
does male-to-female discrimination compare with female-to-male discrimination? Our main
results, presented in Section 3, are as follows. (1) We find a moderate tendency towards
discrimination against the out-group, with a majority of null results across the
literature. (2) The strength of discrimination against the out-group does vary according
to the type of group identity subjects are divided by. It is greater when identity is
artificially instilled in a subject pool than when it is divided by nationality or
ethnicity – minimal groups, it seems, are not so minimal after all. Discrimination is even
stronger, though, when participants are divided into socially or geographically distinct
groups. (3) The extent of discrimination against the out-group also depends on the role
participants are given in an experiment: when subjects are asked to allocate payoffs
between inactive players belonging to the in-group and out-group, it is stronger than in
any other decision-making context. (4) Students do not appear to be differently inclined
towards discrimination than non-students. (5) We find evidence in support of both taste-
based and statistical discrimination. Tastes appear to drive the general tendency for
discrimination against the out-group, but individual studies have found beliefs to affect
discrimination. (6) In gender discrimination experiments the tendency for discrimination
against the out-group is reversed, as subjects demonstrate slight but significant
favouritism towards the opposite gender. Discriminatory behaviour in these experiments
does not differ significantly between males and females. We discuss possible
interpretations of these results in depth in Section 4. We are aware of only one other
meta-study attempting to analyse the experimental discrimination literature – Balliet et
al. (2014),2 who take 214 estimates of discrimination from 78 studies. There is little
overlap between our samples; Balliet et al. take studies from across the social sciences
but their search and inclusion criteria result in most of the experimental economics
literature on discrimination not being included (26 of our studies – around a third –
feature in Balliet et al.׳s sample). They exclude decision-making contexts which we
consider, such as being the second mover in a sequential game or a third-party allocator.
They also exclude interactions between gender groups. The present study and that of
Balliet et al. can be viewed as complements. Through focusing only on economic
experiments, we enhance comparability and eliminate some studies using methodological
elements that may not be acceptable to some social scientists. Our focus on the economic
theories of taste-based and statistical discrimination differentiates our study from
Balliet et al., who investigate psychological theories of discrimination. Throughout our
analysis we compare our results to theirs. Their paper finds a similar overall tendency
for discrimination to what we do. They find the extent of discrimination not to differ
significantly between settings of natural and artificial identity, but do not split
natural identity into subcategories as we do. The clearest difference in results between
the two studies is that Balliet et al. find discrimination is stronger by decision-makers
who move simultaneously than by first movers in sequential exchanges, while we do not find
it significantly differs between these settings.

<h>METHODOLOGY AND CRITERIA FOR INCLUSION</h>
--------------------------------------

We chose to restrict our study to the experimental economics literature. Almost all of the
economics experiments have been conducted in the last 15 years and can reasonably be
expected to have followed comparable procedures, which is important in a meta-analysis. We
define an economics paper as follows: it must either have been published in an economics
journal or have as at least one of its authors a person trained in economics or a
business-related discipline, or who has at least once held a position in an economics or
business-related department. Furthermore, we exclude economics papers which, it is clear
to the reader, exhibit a breach of standard experimental economics practice – most
notably, deception. For inclusion, an experiment must involve interaction between
individuals whose decisions determine real material payoffs for participating players. In
other words, it must be incentivised. A serious pitfall meta-analyses can face is
publication bias, also named the ‘file drawer problem’. Because null results are less
likely to be published than significant ones, a meta-analysis risks including a
disproportionately low number of studies finding small or no effects (Rosenthal, 1979;
Rothstein et al. 2006). This can lead to an overestimation of average effect sizes. It can
also, if null results are particularly unlikely to be published when combined with certain
other features of a study, result in the meta-analysis overestimating the relationship
between strong effects and these features; in our case, for instance, if null results in
trust games were never published but null results in other games sometimes were, we would
be in danger of estimating a spuriously strong relationship between trust games and
significant results. To minimise such bias, a good meta-analysis should conduct the most
thorough literature search possible in order to find all applicable studies, whether
published or not. Our approach was threefold. In late 2013, we conducted RePEc searches
for the keywords, ‘Discrimination experiment’, ‘Identity experiment’, ‘Ingroup experiment’
and ‘Outgroup experiment’, and carefully sifted through the output for candidate studies.
We then followed the references and citations of all papers identified as relevant.
Finally, we checked our list of included studies against that of Balliet et al. (2014);
this step added one study (Spiegelman, 2012).3 One feature of the literature we meta-
analyse is that studies tend to include various different treatments, and therefore report
multiple results. This may act as a further curb on publication bias – insignificant
findings make their way into papers alongside more interesting significant results
(indeed, it turns out the majority of results in our dataset are null).4 Previous meta-
analyses in experimental economics such as Engel (2011) and Johnson and Mislin (2011),
which focus on a single game type, are able to use the average behaviour of subjects
(amount sent in the dictator or trust game) as a continuous dependent variable, with one
observation and an associated standard error for each treatment. In our case, we are
pooling across different game types and therefore need a way of transforming the data to
make meaningful comparisons between these settings. Our variable of interest is the
difference between decision-makers׳ behaviour towards their in-group and their out-group,
whilst all other aspects of the experimental design are held constant – in essence, the
discrimination effect size. There is typically one observation per every two treatments
(one in-group and one out-group treatment) for each type of player active in the given
game. The exception is when a decision-maker interacts with both the in-group and the out-
group in the same treatment (either by making one decision which simultaneously affects
both, or by playing in the same role twice), in which case a within-treatment measure of
discrimination is available.5 The ideal approach would be to record an effect size for
each comparison, and we attempt to do this. Consistent with Balliet et al. (2014), the
measure we use is Hedges׳ unbiased d: the mean difference in behaviour towards the in-
group and the out-group, divided by the pooled standard deviation, with a minor correction
for sample size (Hedges and Olkin, 1985). However, a substantial number of studies do not
report sufficient data for us to calculate effect sizes. This is particularly the case
with null results, as when a difference is not significant authors are less likely to
report the test statistic from which an effect size could be derived. We sent data
requests to the authors of all papers for which we could not construct the measure using
information provided in the paper. After receiving data from 22 of the 36 sets of
contacted authors, we ended up with effect sizes on 364 of our 441 data-points. We
therefore also employ a binary dependent variable, recording simply whether, for each
comparison, behaviour significantly favours the in-group over the out-group at the 5%
level.6 The effect size is the inferior dependent variable in that it restricts the sample
and may lead to greater under-representation of null results; but the superior one in
terms of information content. For simplicity, we define ‘discrimination’ as discrimination
against the out-group, and ‘out-group favouritism’ as discrimination against the in-group,
and will use these terms hereafter. Unlike some, we make no distinction between nepotism
and discrimination; any result of favouritism towards one group relative to a second can
equivalently be interpreted as discrimination against the second group. We therefore
conceptualise ‘discrimination’ (against the out-group) as something which can be measured
on a continuum with positive and negative values. When discussing average effect sizes, we
will describe a relatively low value as indicating ‘lower’ or ‘weaker’ discrimination,
even if it is driven by highly negative effect sizes (i.e. even if it is driven by
instances of strong discrimination against the in-group). For an observation to meet our
inclusion criteria, there must be an in-group and out-group, clearly defined on the basis
of categorisation by a discrete identity-relevant variable, such as ethnicity, gender or –
as with artificial groups – the preference for a particular artist or the colour randomly
drawn. There must be controlled interaction within and between the groups, and decision-
makers must be aware that they are interacting with individuals belonging to their in-
group or out-group. We only consider an in-group to be appropriately defined as such if
every one of its members shares the same categorisation as the decision-maker on the basis
of the relevant variable. For an out-group to be appropriately so-defined, every member
must take a different categorisation from the decision-maker. It is not required that all
members of an out-group take the same categorisation as each other. For instance, Guillen
and Ji (2011) use as their two groups Australian and non-Australian. In this case, for an
Australian decision-maker the Australians are the in-group and the non-Australians the
out-group, but for a non-Australian the other non-Australians should not count as their
in-group. We then only record the observed behaviour of the appropriately defined group,
the Australians in this example. Occasionally, we are forced to make a subjective decision
on what can reasonably be considered a group. For example, from Chen et al. (2011), which
splits its US-based sample into white and Asian students, we record the behaviour of the
white ‘group’ but not that of the Asians, as we believe that in American society white
people can appropriately be defined as comprising a shared ethnicity, whilst those of
Asian descent comprise a mixture of ethnicities.7 Papers such as Falk and Zehnder (2007)
which do not have clear groups but measure each subject’s position on a scale of social
distance, based on a continuous variable, are not included. If an experimental design
splits the sample up into more than two separate groups, on the basis of a single
identity-relevant variable, we record separately how each group treats each other group
relative to its own. If such a paper reports that Group A does not significantly
discriminate against Group B or Group C but does significantly discriminate against Groups
B and C combined, we record two results of no discrimination rather than one result of
discrimination; and in the main text of this paper we report our results using this
approach. We do this because, although Groups B and C combined could represent a single
out-group as defined above, the experiment was set up to treat them as separate out-
groups. Similarly, we do not include the reported results of statistical tests run on data
pooling two or more treatment pairs. These are grey areas but we have re-run our main
regression results for the binary dependent variables in the case of treating every result
reported in our sample as an observation: this adds 16 extra data-points and does not
qualitatively change our findings. Sufficient data must be reported for it to be clear
whether there is significant discrimination in each pair of treatments (or, when
applicable, single treatment); if we cannot work out whether there is discrimination in
one or more treatment pair, the whole paper is omitted from the study. This is because
papers are less likely to report the results of statistical tests finding no
discrimination, and if we failed to include a given study’s non-results our analysis would
overestimate the likelihood of this particular design finding discrimination. For similar
reasons, if an experiment employs a cross-cutting design, dividing its subject pool by
multiple identity types, it must report whether there is discrimination on the basis of
each category. For example, an experiment which segregates the subjects by both gender and
ethnicity must report, for each applicable treatment pair, whether each ethnic group
discriminates against each other ethnic group or not, and also whether each gender
discriminates against the other or not. Otherwise, we omit the study. Experimenters using
artificial groups generally conduct tests on pooled data; rather than reporting whether
Group A discriminates against Group B and vice versa, they report whether individuals
across the sample pool discriminate against out-group members. This makes sense because
there is no obvious reason to doubt the relationship between two artificial groups is
completely symmetrical. As such, we use pooled discrimination observations for artificial
group experiments. Using similar reasoning, we also admit pooled discrimination
observations for experiments dividing subjects by their real-world social groups. The
pooling of certain types of data might lead to an increased chance of finding
discrimination in certain experiments, which is one reason why we use the size of the
sample from which the result is derived as a control variable in our regression analysis.
We limit our analysis to lab and lab-in-the-field experiments; we do not include pure
field experiments, in which subjects do not know they are participants in a study. We
therefore do not include the large body of field experiments in which applications are
sent to employers, landlords or others to test for discrimination in markets
(correspondence studies).

<hs>  Analytical methods</hs>
  ~~~~~~~~~~~~~~~~~~

Listed in the next subsection are descriptions of the independent variables we include in
our regressions. Our basic model contains role and identity type dummies, and some
controls. Because our samples are not large and most variables are dummies, we regard
linear probability models (LPMs) with errors corrected for heteroskedasticity as the best
specifications when employing the binary dependent variables. However, we also run as
robustness checks logit models, which we report in Appendix C, Table C.2. In some cases
the logits drop observations, which is a major disadvantage. Their results, however, are
qualitatively similar to the LPMs. When using binary dependent variables, we treat each
study within the meta-analysis as providing a cluster of observations. When analysing the
continuous dependent variable, we first use standard random effects meta-analysis
procedures to determine average effect sizes for our full sample and for the subsamples
based on identity type. These are simply aggregate estimates for the level of
discrimination in the relevant subsample; they do not control for independent variables.
The procedure takes into account that each observation has an associated standard error.
It weights each observation by the inverse of this standard error, thus attaching more
importance to results from larger samples and with smaller standard deviations. It then
follows an unweighting process, the extent of which depends upon the heterogeneity in
effect sizes. The more heterogeneity there is across effect sizes, the more equal will be
the weights attached to observations with small or large standard errors (Harbord and
Higgins., 2008).8 We then apply random effects meta-regressions, which allow the inclusion
of independent variables in the analysis. These models follow the same processes of
weighting and unweighting observations as described in the previous paragraph, but are
otherwise standard linear regressions. Whereas with the binary dependent variable we must
approach discrimination and out-group favouritism separately, the meta-regression analyses
both simultaneously, since the effect sizes can be positive or negative. This can be one
reason why the results of the meta-regressions may differ from those of the linear
probability regressions. Another can be the reduction in sample – therefore, when the
results of the meta-regressions do not match those of the LPM regressions on
discrimination, we present the LPMs re-run on the reduced effect-size sample, in order to
determine whether the disparity is due to the change in sample or the change in analytical
approach.

     <hss>Role type dummies</hss>

        We include role type dummy variables to pursue the question of how different
        decision-making contexts affect the extent of discrimination. The games used in
        this literature feature either multilateral or unilateral decision-making. When
        decision-making is multilateral, the outcome of the game is determined by more
        than one player׳s actions. From such situations, we identify three different role
        types: First Mover (140 observations), where one׳s move does not finish the game;
        Second Mover (119 observations), where one determines the final payoffs in
        response to the co-player(s)’ actions; and Simultaneous Mover (66 observations),
        where one makes the last move of the game at the same time as one׳s co-player(s).
        When decision-making is unilateral, the final outcome of the game is determined by
        one player. From these situations, we identify a further three role types. First,
        there is the Dictator (67 observations), who allocates payoffs between another
        player and his- or herself. Next we have third-party allocators (Allocator, 30).
        These are players who must divide a pie between two or more passive players (who,
        in these experiments, are members of different groups), but whose own payoff does
        not depend on this decision. Finally, there are players tasked with selecting a
        partner (from a choice of in-group and out-group participants) with whom to play a
        subsequent game. We label this role Partner Chooser (19 observations).9

     <hss>Identity type dummies</hss>

        A second set of dummy variables records which type of group identity a given
        experimental sample has been divided according to. We consider identity to have
        been artificially induced if researchers split subjects into groups that, prior to
        the experiment, did not exist – in the sense of group members sharing
        characteristics that are not also shared by members of other groups in the study –
        and the subjects are aware they have been split into these groups.10 49 studies in
        the meta-analysis investigate natural identity, 32 artificially generate it, while
        the remaining four contain both natural and artificial treatments. We have 272
        observations for natural identity types and 169 for artificial. We subdivide the
        natural observations into six specific categories of natural identity. First, we
        have 82 observations from 13 studies in which subjects are divided by Nationality.
        Next, nine studies investigate Ethnicity-based identity, adding 63 observations. A
        further seven studies generate 32 observations on Gender identity. 21 more
        observations are provided by five studies in which the subjects are split by
        Religion. 13 studies use a rather different approach, dividing the subject pool
        into groups based on real-world social and/or geographical identity. This is done
        in a variety of ways: for instance, using villages (Dugar and Shahriar, 2010),
        colleges within universities (Banuri et al., 2012) or friendship groups (Brandts
        and Sola, 2010). However, all such designs share the common feature that each
        decision-maker has a clearly distinct social and/or geographical in-group – group
        identity here is defined with reference to the relative frequency with which one
        interacts with in- and out-group members in ordinary life. The 57 observations
        generated by these experiments are coded under the variable Soc/Geo Groupings. The
        remaining 17 results, from four papers, deal with other types of natural identity,
        which cannot appropriately be fitted into the above categories. These observations
        relate to political identity (Abbink and Harris, 2012), disability (Gneezy et al.,
        2012), caste (Hoff et al., 2011) and whether farmers are private or members of
        cooperatives (Hopfensitz and Miquel-Florensa, 2013). We pool them under the
        composite variable Natural Other. 11,12

     <hss>Other variables</hss>

        In our regressions we include as a dummy variable (Students) whether each
        observation derives from a sample consisting predominantly of students or non-
        students. Even if not explicitly stated, we assume experiments run at universities
        have at most a very small number of non-student participants. Likewise, while we
        accept experiments in the field may include a few student subjects, their
        proportion is likely to be low (unless otherwise stated). As another control, we
        include the size of the active decision-making sample from which a given result is
        derived (Sample Size).

<hs>  What is the general pattern of discrimination across the literature?</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In total, as shown in Fig. 1, there are 144 results indicating significant discrimination
(32.65%), 28 indicating significant out-group favouritism (6.35%), and 269 indicating no
significant discrimination or out-group favouritism (61.00%). 57 of our 77 studies record
at least one result of discrimination, while only 15 record any results of out-group
favouritism. 10 studies separately record results of discrimination and out-group
favouritism. The general tendency, then, leans towards insignificant results, although
only 15 studies consist entirely of nulls. For the sub-sample where we are able to
generate effect sizes (364 of 441 observations), the random effects meta-analysis finds an
overall effect size of 0.256 (95% confidence range: 0.209–0.304). This can be interpreted
as, on average, subjects׳ discriminating against out-groups by about a quarter of a
standard deviation. This is not significantly different from Balliet et al. (2014), who
find an overall effect size of 0.32 (95% confidence range: 0.27–0.38). Fig. 1 also
displays point estimates for aggregate effect sizes, conditional on the type of result
found for each observation. Observations finding significant discrimination have an
average effect size of 0.67, those yielding null results have an average effect size of
0.11, and those finding significant out-group favouritism have an average effect size of
−0.51; this confirms that the strength of the effect size tends to be closely related to
the type of result found for a given observation. : In general, there is limited
discrimination against the out-group.

<hs>  How does the level of discrimination vary according to the type of identity groups are based upon?</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Table 1 displays a breakdown of our sample׳s observations by identity category, and the
results of random effects meta-analyses run on these sub-samples. For most categories the
tendency is towards null results. Only for Soc/Geo Groupings – which yields no results of
out-group favouritism – are observations of discrimination more likely than insignificant
results, and this is also the identity type with the highest average effect size. The
category for which there is least discrimination and most out-group favouritism is gender;
the average effect size for this sub-sample is negative. Table 2a extends the analysis of
Table 1 through the use of regressions. LPMa is a linear probability model with the
dependent variable discrimination against the out-group (equal to 1 if discrimination is
found, 0 otherwise). Metareg is a meta-regression with the dependent variable the
discrimination effect size. In both models artificial identity and the dictator game are
the benchmark categories.13 In these regressions we test whether our identity-type
variables still yield significantly different levels of discrimination after controlling
for other factors. Table 2b presents the results of linear restriction tests run on the
sets of dummy variables featuring in the models. In both the linear probability models and
meta-regression, the identity category linked to the strongest discrimination is social
and geographical groupings. In Metareg it yields significantly higher discrimination, at
the 1% level, than any of the other identity categories. In LPMa it does the same, except
that the differences with Artifical and Natural Other are only significant at the 5% and
10% level respectively. The identity category linked to the weakest discrimination is
gender. Both the linear probability model and the meta-regression indicate weaker
discrimination between genders than between artificial groups, significant at the 1%
level. The meta-regression also finds gender discrimination to be weaker than ethnic and
national discrimination (at the 1% level), and religious discrimination (at the 10%
level). However, LPMa does not find these differences to be significant.14 In LPMa the
coefficients on the ethnic and national identity types are significantly negative at the
1% level, strongly indicating that discrimination is less likely to be observed when
subject pools are split along these lines than on the basis of artificial identities.
According to Metareg, however, ethnic and national identity experiments are only linked to
significantly lower discrimination (i.e. less positive effect sizes) than artificial group
experiments at the 10% level. Given the inconsistency, Table 2a also reports LPMb, a
linear probability model run on the reduced sample for which effect size calculation is
possible. This helps to distinguish whether the losses of significance when moving from
LPMa to Metareg are due to the reduction in sample or the change in measurement technique.
For the comparison of national and artificial identity, the loss of significance appears
to be due to the change in sample, as in LPMb the coefficient is also insignificant. The
same cannot be said for Ethnicity, however, as the linear probability model on the reduced
sample continues to report significantly less discrimination between ethnic than
artificial groups at the 1% level. Doubt, therefore, is cast over the robustness of our
finding on ethnicity – although the coefficient’s sign is at least weakly
significant.15,16 The strength of discrimination depends upon the type of group identity
under investigation. It is stronger when identity is artificially induced in the
laboratory than when the subject pool is divided by ethnicity or nationality, and higher
still when participants are split into socially or geographically distinct groups.

<hs>  How does the level of discrimination depend upon the decision-making context?</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Inspection of the coefficients on role type dummies in LPMa and Metareg (Table 2a) reveals
discrimination is significantly stronger when the decision-maker is a third-party
allocator than when he or she is a dictator (the omitted category). Linear restriction
tests (Table 2b) also show the third-party allocator role is more likely to be associated
with discrimination than all the other role types, with the difference always significant
at the 1% level under both models. The size of the Allocator coefficients in the meta-
regression (1.077) is worth noting – it indicates that discrimination in games of this
type tends to be very large indeed, with on average more than one standard deviation
between subjects׳ treatment of in- and out-groups. The other role types do not carry
significantly different effects from one another. This is at odds with Kiyonari and
Yamagishi (2004) and Balliet et al. (2014), who find discrimination to be stronger by
simultaneous movers than first movers (Balliet et al. do not investigate second movers).
In an attempt to discern why our result differs from that of Balliet et al., we re-ran our
analysis keeping only the observations included in their study. We found there was still
no significant difference between First Mover and Simultaneous Mover (the remaining sample
on which to run this regression was small; however, we also compared the aggregate effect
sizes for each category and found they are very similar). This suggests the significance
of the finding in Balliet et al. is driven by studies outside our dataset, i.e. outside
the economics literature.17 Third-party allocators discriminate more than decision-makers
in all other roles.

<hs>  Do students discriminate any more or less than non-students?</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Most decision-makers in our analysis were students. Only 101 observations, from 22
studies, are produced by in-groups not comprised (at least in their near-entirely) of
university students. 31.8% of the observations for students return discrimination, while
6.8% find out-group favouritism and 61.5% are null; for non-students 35.6% find
discrimination, 5.0% yield out-group favouritism and 59.4% are null. The coefficient on
Students is not significant in any of our regressions. That experiments with students do
not generate significantly different levels of discrimination than those with non-students
is an interesting non-result which suggests that, in this literature, working with student
samples will not generate a biased perception of the extent and magnitude of
discrimination by the wider population.18 : Discrimination does not significantly differ
between students and non-students.

<hs>  Does the experimental literature provide more support for taste-based or statistical theories of discrimination?</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

For 262 (59.4%) of our observations, as a result of the experimental design any
discrimination must be taste-based, as it cannot be statistical. Statistical
discrimination cannot occur when a player is making the only or last move in a game,
unless the game is to be repeated, or possibly if the move is made simultaneously with
others. Discrimination by trust game returners, for example, can only be taste-based,
because opponents then have no control over the final outcome and beliefs about their type
are therefore irrelevant.19 All observations under the Dictator and Allocator categories
preclude the possibility of statistical discrimination, as do all except seven (due to the
game being repeated) in the Second Mover category. All observations under the First Mover
category permit the possibility of statistical discrimination, as do most in the Partner
Chooser category and around a third in the Simultaneous Mover category.20 In Table 3, we
run a linear probability regression on discrimination and a meta-regression on the
discrimination effect size, with role types re-coded into two types: one,
Taste+Statistical, where there is scope for both taste-based and statistical
discrimination, the other (the omitted category) where there is scope only for taste-based
discrimination. Note that in this literature any game-role contains scope for taste-based
discrimination. The coefficient on Taste+Statistical is positive but insignificant in both
the linear probability regression (p=0.87) and the meta-regression (p=0.18). This
indicates there is no significant difference in the likelihood of observing
discrimination, or in the predicted effect size, when scope for statistical discrimination
is added.21 This would suggest taste-based discrimination is an important driver of
behaviour in these experiments and statistical discrimination is not, but we probe further
by analysing the results of individual experiments. Where there is scope for
statistically-motivated discrimination, by design for 66.5% of these observations it is
not possible to disentangle its effects from taste-based motivations. To be able to do so,
an experiment must either use belief elicitation or include a control game in which
behaviour can only be taste-based – the most common case of this is adding a dictator game
to extricate taste-based from statistical discrimination by trust game senders.22 In the
60 cases that it is possible to distinguish between discriminatory motives, the authors
find significant statistical discrimination to occur in 13 cases (10 times against the
out-group and three times in favour of it). Within the same sample, for given beliefs or
behaviour in a game with a belief-based component, they find significant taste-based
deviations from own-payoff-maximisation in 26 cases (16 times against the out-group and 10
times in favour of it). In 26 cases neither statistical nor taste-based discrimination is
found at the 5% level. We list all significant findings of taste-based and statistical
discrimination from experiments designed to distinguish between the two in Appendix A,
Table A.3. Although the sample is small, tastes are found to affect behaviour more often
than statistical beliefs. It seems, however, that beliefs do play some role in determining
discriminatory behaviour in economics experiments. We conjecture that the insignificant
regression results in Table 3 may be due to the fact that beliefs can either increase or
reduce discrimination. This would be because individuals have favourable beliefs about the
cooperativeness of out-groups, or because unfavourable beliefs about the out-group׳s
cooperativeness can in some cases actually lead to statistical out-group favouritism. That
is, depending on the game setting, self-serving optimal behaviour can either become more
or less generous in response to the perception that one׳s partner is relatively
uncooperative. In ultimatum games, for instance, if proposers expect out-group responders
to treat them less favourably than in-group responders do, the self-serving optimum is to
send them relatively kind offers. This is in contrast to how first mover behaviour would
work in trust games, say, where a self-serving sender will send relatively low investments
to an out-group responder if it expects to be treated unfavourably by them.24,25 : There
is evidence for both taste-based and statistical discrimination. Tastes appear to drive
the general tendency for discrimination against the out-group, but individual studies have
found beliefs to affect discrimination.

<hs>  In gender experiments, how does male-to-female discrimination compare with female-to-male discrimination?</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

An immediately obvious finding is that gender acts very differently from other identity
types. It is the only identity category which is more likely to be associated with a bias
against the in-group than against the out-group, with eight results of the former and
three of the latter out of a total 32 observations. On the reduced sample, the random
effects meta-analysis finds an overall discrimination effect size of −0.177 (95%
confidence range: −0.301 to −0.053) for gender experiments, representing significant out-
group favouritism. There is obvious intuition why gender is different from the other
identity categories: it is the only case in which the effects of sexual attraction –
towards the out-group more than the in-group, for most subjects – and ׳chivalry’ (Eckel
and Grossman, 2001) can be expected. Every experiment on gender in the meta-analysis has a
symmetrical male-female design, meaning that for every estimate of discrimination by men
against women there is an identical treatment measuring discrimination by women against
men. This allows a very clean comparison of these two behaviours across the sample. The
only three significant results in our dataset of one gender discriminating against the
other are female decision-makers discriminating against males, while six of the eight
significant results of one gender favouring the other are male decision-makers favouring
females. However, the calculated overall effect size for female decision-makers is
actually slightly more negative than for males: −0.181 (95% confidence range: −0.35 to
−0.013) for females and −0.173 (95% confidence range: −0.369 to 0.024) for males, although
the difference is far from significant. Note that while the effect size indicates females
significantly favour males at the 5% level, the equivalent effect for male decision-makers
is only significant at the 10% level. : There is significant out-group favouritism in
gender experiments. Females significantly favour males; males favour females but the
effect is only weakly significant.

<h>DISCUSSION AND CONCLUSIONS</h>
--------------------------

A leading result of this paper is that discrimination in economics experiments varies by
the type of identity groups are based upon. It is very strong when groups are socially or
geographically distinct, and is relatively weak when they are based on ethnicity or
nationality. Notably, it tends to be relatively strong in experiments using artificially-
induced group identities – so it can confidently be stated that minimal groups do not
produce the minimal level of discrimination. At first glance, this seems surprising. It
might be that artificial group manipulations are stronger priming instruments than natural
identity experiments tend to use – after all, these dedicate an entire preliminary phase
of the experiment to inducing feelings of identity, which will remain at the front of
subjects׳ minds when they are then offered the chance to discriminate. This explanation is
arguably supported by the evidence of Robbins and Krueger (2005), whose meta-analysis of
psychology experiments shows subjects exhibit stronger in-group projection – that is, they
perceive in-group members to be particularly similar to them, relative to out-group
members – when identities are artificial than when they are natural. On the other hand, we
do not find that team-building exercises, which are designed specifically to strengthen
artificially-induced identity and would seem to amplify priming, have a significant effect
on the level of discrimination (this is consistent with the findings of Chen and Li
(2009)). Conversely, it could be argued that, for the populations studied in the
literature, membership of particular ethnic and national groups does not actually instil
strong identity, so that even such trivial identities as can be artificially induced have
a greater effect. There is evidence that the process of globalisation has weakened
national and ethnic parochialism (Buchan et al., 2009), and in recent decades youth
identity in the West and increasingly elsewhere has come to define itself to a large
extent upon individuals’ belonging to subcultures based on fashion and music tastes –
preferences drawn from choice sets which are not, indeed, so different from the apparently
arbitrary minimal group painting dichotomy. However, it would seem highly complacent to
draw the conclusion from our results that racism and xenophobia are not big problems in
many societies. Another explanation may be that subjects in ethnic and national identity
experiments are shying away from displaying ׳politically incorrect’26 behaviour, given
that racism and xenophobia are taboo in most societies today. While the link between
social acceptability and discrimination has not been well explored, the prejudice
literature has yielded relevant findings: that expressions of prejudice correlate with
perceptions towards the social acceptability of such prejudice (e.g. Crandall et al.,
2002), and furthermore that this correlation is at least partly the result of norm-
compliance (e.g. Blanchard et al., 1994). It seems unlikely that discriminating on the
basis of a stated preference for Klee׳s paintings over Kandinsky׳s carries any taboo
similar to ethnic or national discrimination. Indeed, some subjects may regard an
artificial group situation as a game in which they belong to one of the teams, wherein the
social norm actively encourages favouritism of one’s own group – the sheer strangeness of
the setting may even lead subjects to perceive a demand for discrimination on the part of
the experimenter (see e.g. Zizzo (2010)). Concerns about social acceptability could
explain also why the Soc/Geo Groupings category produces significantly higher
discrimination than other types of natural identity. Of course, it would not be surprising
if relational and geographic proximity led to a stronger sense of belonging than shared
ethnicity, religion or nationality, but bear in mind too that there is arguably no taboo
against favouring friends over strangers.27 If it were shown that discrimination in
economics experiments is indeed limited by concerns about social acceptability, it might
cast doubt over the external applicability of such studies׳ findings. It is possible that
if participants guess an experiment is about a type of discrimination which is taboo, it
will systematically generate a lower effect than if the subjects were unaware of its
purpose. On the other hand, the very same concerns about social acceptability might also
limit certain types of discrimination outside the lab. It is noteworthy that gender is the
identity category producing the weakest discrimination: in fact, here the meta-analysis
finds a significant amount of out-group favouritism. However, gender discrimination
clearly persists in the outside world. It may be that economics experiments do not find it
because they poorly reflect the conditions under which it survives beyond the lab – in
particular, in the job market. It would be interesting to see more experiments designed to
directly compare the effects of different types of group identity. This meta-analysis
includes just four. Dugar and Shahriar (2009), Li et al. (2011) and Goette et al. (2012a)
all compare discrimination between social/geographical groups and artificial groups, while
Abbink and Harris (2012) use artificial groups and political groups (which fall under the
Natural Other category). The results of all four studies are consistent with ours –
discrimination is always lower with artificial identity. However, direct comparisons
between artificial group and ethnic or national discrimination are lacking, and it would
be very illuminating to see whether such studies support – and if so, whether they can
explain – the findings of this meta-analysis. What implications does our research have for
future experiments on discrimination? First, using artificially induced identities as a
control against which to pit the results of natural identity treatments may not be
recommendable, as the artificial group manipulation appears not so much to capture the
minimal level of discrimination that must result from priming any type of identity in a
laboratory as to in fact often go beyond that. Regarding role type, we find discrimination
by third-party allocators is much stronger than by participants in any other game setting.
If social acceptability does indeed limit discrimination, this is a counterintuitive
result, as the allocator role essentially invites subjects to overtly and consciously
favour one group over another and therefore seems to be the one that most obviously
telegraphs the purpose of this type of experiment. One possibility is that the role
carries an experimenter demand effect – whereby subjects feel they are encouraged to
discriminate – or even an action bias effect, if the equal split feels like a default non-
move. Another relevant factor may be that the third-party allocator is unique amongst our
role types in the decision-maker׳s payoff being entirely disconnected from the extent to
which they discriminate. In any case, experimenters should bear in mind that because they
are more likely to identify significant discrimination when they employ the allocator
role, they should be less confident that the same groups will discriminate against each
other in different contexts. We find the strength of discrimination does not significantly
differ between student and non-student subject pools. This suggests – unlike in the
context of social preferences (e.g. Bellemare and Kroger, 2007; Anderson et al., 2013) –
student subjects are not a generally unrepresentative sample for questions relating to
discrimination. However, we do not exclude the possibility that they are unrepresentative
in specific instances, or within particular societies. There is scope for more
experimental research investigating taste-based and statistical discrimination. We show
both are relevant, and the two types manifest themselves to different extents in different
contexts. However, relatively few experiments have been designed to distinguish between
taste-based and statistical discrimination, and more could be known about the mechanisms
underlying them. As a final observation, there is a great deal of variation in the
findings of the experimental economics discrimination literature. Our analysis can explain
some of it, but our LPM regressions typically have R2 statistics below 0.2, and the meta-
regressions׳ Adjusted R2s are rarely above 0.35. As might be expected, discrimination does
seem to vary idiosyncratically and is not easy to predict. The results of natural identity
experiments do not seem very generalizable – they probably reflect more the
characteristics of the specific groups under investigation, and the relationships between
them, than aspects of the experimental design. Whilst a drawback for some research
questions, this also means there is a great deal of scope for future experimental studies
aimed at measuring the levels of discrimination within subject pools of specific interest.
Furthermore, given the potential concerns we raise about experimenter demand effects and
the external validity of lab experiments on discrimination, the important role of field
experiments should be emphasised. Subjects in such studies are unaware they are being
observed by experimenters and their behaviour can therefore not be influenced by the fact.
Field experiments can test the generalisability of lab findings on discrimination.


<h>REFERENCES</h>
----------

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<ART>Does competition from private surgical centres improve public hospitals’ performance? Evidence from the English National Health Service
================================================================================

Authors: Zack Cooper, Stephen Gibbons, Matthew Skellern
DOI: 10.1016/j.jpubeco.2018.08.002
Year: 2018  |  Pages: 63-80
ASJC codes: 2002, 2003
Keywords: Cream skimming, Hospital competition, Hospital efficiency, Market entry, Market structure, Outsourcing, Public services, Public-private competition, Risk selection

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper examines the impact of a government programme which facilitated the entry of for-profit surgical centres to compete against incumbent National Health Service hospitals in England. We examine the impact of competition from these surgical centres on the efficiency – measured by pre-surgery length of stay for hip and knee replacement patients – and case mix of incumbent public hospitals. We exploit the fact that the government chose the broad locations where these surgical centres (Independent Sector Treatment Centres or ISTCs) would be built based on local patient waiting times – not length of stay or clinical quality – to construct treatment and control groups that are comparable with respect to key outcome variables of interest. Using a difference-in-difference estimation strategy, we find that the government-facilitated entry of surgical centres led to shorter pre-surgery length of stay at nearby public hospitals. However, these new entrants took on healthier patients and left incumbent hospitals treating patients who were sicker. This paper highlights a potential trade-off that policymakers face when they promote competition from private, for-profit firms in markets for the provision of public services.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

In the 2000s, there was a widespread push in Europe and the United States to increase the
role of user choice and provider competition in public services. In general, these pro-
market reforms were designed to increase the quality and efficiency of public services
like health care and education, which had previously been run through non-market means
like performance management (Gaynor and Town, 2011; Propper et al., 2007, 2010). Often, as
part of these market-based reforms, policymakers encouraged the entry of private, for-
profit firms to compete against public sector providers. These efforts are exemplified by
the growing use of charter schools in the United States and private health care providers
in publicly funded health systems in Western Europe (Jost et al., 2006; Fryer Jr, 2012).
This paper explores how competition generated by the government-facilitated entry of
private, for-profit firms affects the performance of incumbent public providers. In
particular, we estimate the impact of the entry of a series of private, for-profit
surgical centres in the English National Health Service (NHS). Policymakers steered the
entry of these surgical centres to areas with high patient waiting times, with the aims of
increasing surgical capacity and stimulating competition. We estimate the impact of this
private provider entry on the efficiency of incumbent public hospitals, and examine
whether it left incumbents with a riskier and more costly mix of patients. Advocates of
diversifying the supply of public services providers argue that private, for-profit
entrants will innovate and offer higher quality than incumbents, and that entry of private
providers will create competitive pressure on public providers to raise their own
performance (Le Grand, 2009; Seddon, 2007). We are particularly focused on testing this
latter claim: can the entry of private, for-profit surgical centres improve the
performance of incumbent public hospitals? Critics of market-based reforms generally cite
the many ways that public services, and health care in particular, differ from highly
stylised, perfectly competitive markets, and argue that competition will not improve
performance (Jones and Mays, 2009; Fotaki et al., 2008). Moreover, it is sometimes argued
that, because new entrants are often much smaller than incumbents (in our case, we analyse
surgical centres competing against hospitals), they may not have sufficient scale to
affect the behaviour of existing providers (Goddard, 2015). A third criticism is that
private, for-profit firms may select customers with desirable characteristics (e.g. better
students or less risky patients), leaving public providers treating a riskier or costlier
group of users (Los Angeles Times Editorial Board, 2016; Bardsley and Dixon, 2011). More
generally, it is not clear that governments are well equipped to determine where to locate
entrants in such a way as to engineer effective competition. The English NHS provides a
unique environment in which to test the effect of private, for-profit provider entry on
public service providers' performance, and in so doing to analyse the extent to which
governments can ‘create’ competition. In the 2000s, the British government facilitated the
entry of Independent Sector Treatment Centres (ISTCs). ISTCs are private, for-profit
surgical centres focused on provision of routine, high volume elective (i.e. medically
necessary, non-emergency, scheduled in advance) surgical procedures to public (NHS)
patients. This policy was part of a wider policy package designed to tackle waiting times
within the English NHS, the centrepiece of which was an ambitious set of targets to reduce
waiting times for surgery. ISTCs were established to rapidly expand capacity in regions
deemed at risk of not meeting these targets (Naylor and Gregory, 2009). As we demonstrate,
while the placement of these specialty surgical centres was correlated with local public
hospital waiting times during the pre-policy period, their placement was uncorrelated with
measures of the efficiency and clinical quality of these incumbents over the same period.
This implies that treatment assignment was unrelated to the pre-policy levels of the
outcome variables we study. In addition, we demonstrate that public hospitals close to
ISTC entrants had nearly identical pre-entry trends to public hospitals unexposed to ISTC
entry across a range of performance measures (other than waiting times). We use this
observation to motivate a difference-in-difference (DiD) strategy to estimate the causal
effect of ISTC entry on outcomes at nearby public hospitals and highlight that our control
group serves a good counterfactual for what would have occurred to the treatment group
after 2004/5 in the absence of the entry of ISTCs. Measuring efficiency of health care
provision is a long-standing challenge because of the absence or poor standard of data on
costs and quality. Faced with these problems, researchers have frequently used patient
length of stay (LOS) as a proxy for efficiency (Fenn and Davies, 1990; Martin and Smith,
1996; Gaynor et al., 2013) on the grounds that, provided clinical quality can be
maintained, shorter LOS implies lower costs for the same outcomes. However, a key
difficulty with using LOS to capture efficiency is that it is heavily influenced by
patient characteristics – patients in poorer health before surgery will tend to have
longer lengths of stay for reasons unrelated to hospital efficiency. In this study, we use
an innovative approach to address the influence of patient characteristics on LOS-based
efficiency measures by disaggregating LOS into two components: time from admission until
surgery (‘pre-surgery LOS’), and time from surgery until discharge (‘post-surgery LOS’).
We show that pre-surgery LOS is less affected by patient characteristics than other
components of LOS, and use it – or alternatively, the percentage of patients treated on
the day of admission – as a proxy for hospital efficiency. In what follows, we show that
the entry of private, for-profit specialty surgical centres led to a 16% reduction in pre-
surgery LOS at nearby public hospitals – which translates to a 24 percentage point
increase in the proportion of patients treated on the day of admission. However, we also
find evidence that these entrants engaged in risk selection, leaving nearby public
hospitals with a sicker (and therefore costlier) mix of patients. In particular, public
hospitals exposed to the entry of private specialty surgical centres experienced an 11.6%
deterioration in average patient health status as captured by the Charlson score (defined
in Section 4). This increase in patient severity likely led to an increase in post-surgery
LOS at incumbent NHS hospitals. Finally, while ISTC entry may have led to reduced case
loads at some public hospitals with which they shared a market, we show that our estimated
treatment effects are not driven by changes in volume caused by ISTC entry. This paper
adds to several literatures. First, it builds on previous work assessing how the entry of
private, for-profit firms impacts the performance of incumbent public service providers
(Hoxby, 1994; Barro et al., 2006; Cutler et al., 2010; Sass, 2006). In general,
researchers have struggled to assess the causal impact of competition from new market
entrants (e.g. surgical centres and charter schools) into markets for public services
because the entry location of private firms is usually endogenous. We exploit the fact
that siting of surgical centres in England was driven by government policy tied to waiting
times, not our efficiency measure, and show that the entry of ISTCs raised incumbent
hospitals' productivity. Second, it adds to the broader literature assessing the impact of
hospital competition (Kessler and McClellan, 2000; Gaynor et al., 2015; Cooper et al.,
2011). We illustrate that, in markets where payments are regulated, competition can raise
hospitals' efficiency. Moreover, we find that smaller entrants can affect the behaviour of
larger incumbents. Third, it adds to the literature analysing whether private, for-profit
surgical centres offering public services risk-select against public incumbents (Barro et
al., 2006; Winter, 2003; Cram et al., 2005; Street et al., 2010; Zimmer and Guarino, 2013;
Bifulco and Reback, 2014). We find that the entry of ISTCs left public hospitals with a
riskier mix of patients. To some extent, this was by design: ISTCs in England were focused
on treating uncomplicated cases. While the entry of specialist surgical centres focused on
routine procedures could in theory represent efficient patient sorting, such an
arrangement is likely to leave existing providers treating a sicker patient mix and worse
off financially, unless it is accompanied by a reimbursement system that adequately
adjusts payments to reflect patient severity. The consensus is that NHS payments were not
adequately risk adjusted during the period we investigate (Mason et al., 2008), meaning
that NHS hospitals that had an ISTC enter nearby were likely left worse off as a result of
being left with a sicker mix of patients. More generally, this paper highlights the trade-
offs that policymakers face when considering policies to encourage the entry of for-profit
firms to compete with public service providers. Facilitating entry can lead to
competition, which can prompt incumbent providers to raise their performance. However,
these for-profit entrants may have very different objectives than incumbent providers, and
may have a higher propensity to risk-select in order to draw a more advantageous mix of
patients. Our work highlights the need for policy-makers to take risk-adjustment of
payments seriously when considering policies to promote competition between firms with
different objectives and differing abilities to treat complicated cases. The remainder of
this paper is structured as follows. Section 2 presents background information on recent
NHS reforms, with particular focus on the ISTC programme. Section 3 explores the potential
impact of ISTC entry on incumbents' performance. Section 4 presents the data and empirical
strategy. Section 5 reports the results, while Section 6 discusses and concludes.

<h>RECENT NHS REFORMS AND THE ISTC PROGRAMME</h>
-----------------------------------------

The English NHS, founded in 1948, is funded through general taxation and, with few
exceptions, offers health care that is free at the point of use. Patients must register
with a single general practice (GP) clinic for the provision of primary care, and GPs act
as ‘gatekeepers’ to the secondary care system. For the most part, secondary care in
England is organised around large public hospitals. The NHS long struggled with waiting
times for elective surgery, which, in some cases, could exceed a year. In 1997, a new
Labour government was elected promising quick action to reduce waiting times. However, 1
year later, waiting times had increased (Klein, 2013, p.200).1 Concerns over waiting times
became the catalyst for a series of reforms from 2000 onwards, which included rigorous
performance management of public hospitals; introduction of patient choice and hospital
competition underpinned by prospective reimbursement; and facilitated entry of specialist
private surgical centres to compete with larger public hospital incumbents. The new
prospective reimbursement system (known as Payment by Results or PbR) was modelled on the
Diagnosis-Related Group (DRG) system used in Medicare in the United States (US). Under
PbR, hospital reimbursement is tied to activity rather than to annual budgets or block
contracts as was previously the case (DH, 2011). In 2000, The Secretary of State released
The NHS Plan (Secretary of State for Health, 2000), in which the government committed to
cutting maximum waiting times for elective surgery from 18 months to 6 months by the end
of 2005 (later reduced to 18 weeks, by 2008) using a series of targets tied to rewards and
punishments. There is substantial evidence that the targets and performance management
regime was extremely effective at reducing waiting times (Propper et al., 2008, 2010;
Besley et al., 2009). As part of its reform programme, in April 2002 the government
announced that it was facilitating the entry of a series of privately run surgical centres
(ISTCs) to deliver routine, high-volume diagnostic and elective surgical procedures to
English NHS patients.2 Like other NHS services, NHS-funded patients could use ISTCs free
of charge. Although the NHS had long made use of private providers in England, ISTCs were
distinctive in three ways. First, they were created as a deliberate policy of government,
as opposed to being a result of decisions by local commissioners of care. Second, they
provided services exclusively to NHS patients, as opposed to earlier arrangements in which
NHS patients were treated in settings mainly focused on treatment of private patients
(Naylor and Gregory, 2009). Third, whereas NHS physicians are in general permitted to also
work in private settings, the first wave of ISTCs (which are the focus of this paper) were
not allowed to use NHS doctors. This restriction ensured that ISTCs represented genuine
new additions to capacity, rather than drawing away physician labour from nearby public
hospitals. More than any other factor, it was local waiting times that influenced where
the government sought to locate the new private surgical centres (HCHC, 2006). According
to government officials, “In October 2002, the Department [of Health] conducted an
extensive forward planning exercise, during which all Strategic Health Authorities were
asked to identify, in conjunction with their respective Primary Care Trusts, any
anticipated gaps in their capacity needed to meet the 2005 waiting times targets. The
results of this exercise led to the identification of capacity gaps across the country,
particularly in specialties such as cataract removal and orthopaedic procedures, where
additional capacity was needed” (Anderson, 2006). Following this planning exercise, in
December 2002 the Department of Health invited expressions of interest to run the first
Wave of ISTCs. These invitations indicated the broad geographical regions within which
ISTCs were to be placed, but left securing a specific site to bidders. Preferred bidders
for these schemes were announced from September 2003. There were 27 Wave 1 ISTCs, all of
which operated on a for-profit basis.3 Of these, 23 opened in 2005 or 2006 (see Fig. 1),
and most operated from a single site, often in newly built premises that were often co-
located with an existing NHS hospital. In March 2005, a second Phase of ISTCs was
announced, of which nine were eventually implemented, with most opening between 2007 and
2008. These Phase 2 ISTCs were smaller, provided a wider range of services including
diagnosis, and were often on the same site as existing private hospitals. Unlike Wave 1
ISTCs, Phase 2 ISTCs were permitted to recruit NHS staff and employ NHS consultants
privately. Phase 2 ISTCs were also required to provide NHS training placements (Naylor and
Gregory, 2009). Given these very different characteristics of the Phase 2 programme, in
this paper we focus exclusively on analysing the impact of Wave 1 ISTCs by excluding NHS
hospitals that were potentially exposed to competition from Wave 2 entrants.4 The ISTC
programme had a major impact on the market for some elective surgical procedures (Naylor
and Gregory, 2009). From 2006, ISTCs accounted for between 5 and 10% of orthopaedic volume
nationally. As the ISTC programme's impact was highly geographically differentiated, the
share of patients attending ISTCs was much higher in some areas than in others. In some
markets where ISTCs entered, they became the only alternative to large incumbents. As one
local NHS official noted when a large ISTC opened next to a dominant NHS hospital, “that's
the first time… we've ever had any competition” (McLeod et al., 2014, p.15). The hope
amongst the policymakers responsible for the ISTC programme was that these entrants would
be less inclined to cooperate with NHS providers, and more inclined to compete (Stevens,
2004). The prohibition on ISTCs employing NHS physicians, and the fact that they were
privately owned, may also have contributed to an institutional culture at ISTCs that was
more receptive to competition than that of public hospitals (Le Grand, 1999). ISTC
contracts specified a range of ‘exclusion criteria’ – acceptable grounds for refusing to
treat NHS patients – on the basis that ISTCs did not possess the emergency or intensive
care units required to treat sicker and more complex patients. Each ISTC had its own list
of exclusion criteria, which typically included demographic factors such as age, social
factors such as availability of a carer at discharge, and clinical factors such as health
status (Mason et al., 2008). In relation to the latter, a particularly important criterion
for rejection was the patient's American Society of Anaesthesiologist's (ASA) score –
ISTCs were typically able to refuse to treat patients with a score of 3 or more.5 National
Joint Registry data from 2010 indicates that, at NHS hospitals, 20% of hip replacement
patients and 19% of knee replacement patients were given ASA scores of 3 or 4. The
corresponding figures for ISTCs were only 6 and 8%, respectively (NJR, 2011). Critics of
the ISTC programme saw these exclusion criteria as particularly problematic because they
allowed the new entrants to dump costlier, more complex patients onto the public hospital
system (Wallace, 2006; Kmietowicz, 2006).6

<h>HYPOTHESES ON THE IMPACT OF ISTC ENTRY ON INCUMBENT PUBLIC HOSPITALS</h>
--------------------------------------------------------------------

This section examines the likely response of public (NHS) hospitals to the entry of
private, for-profit surgical centres (ISTCs). In understanding the impact of the ISTC
programme, it is important to note that, although public NHS hospitals are run on a not-
for-profit basis, they are financially and managerially independent of central government,
and during this period had strong incentives to generate a financial surplus, or at least
not to make substantial losses. In the early 2000s, the government introduced a system of
‘star rating’ of NHS hospitals, in which financial performance was a major factor (Bevan
and Hood, 2006a, 2006b; DH, 2002). Hospitals given a zero-star rating were ‘named and
shamed’, and their chief executives were at risk of losing their jobs. Later, high-
performing hospitals (those with Foundation Trust status) were given additional freedoms
to retain financial surpluses across financial years. Other hospitals were eventually able
to achieve Foundation Trust status in part through good financial performance. These
factors meant that, during this period, public hospitals had a strong incentive to
generate operating surpluses. It has therefore been argued that it is reasonable to think
of public hospitals during this period as maximising profits plus some additional term
reflecting altruistic valuation of quality and/or quantity (Gaynor et al., 2013).
Ultimately, Wave 1 ISTCs differed from public hospitals in three key dimensions. First,
they were explicitly for-profit ventures. Second, they were narrowly focused on offering a
small range of elective surgical procedures. Third, given their inability to hire NHS
staff, their institutional cultures may have differed sharply from those at NHS hospitals.
In what follows, keeping in mind these three differences, we present hypotheses about the
response of NHS hospitals to the ISTC programme.

<hs>  Efficiency</hs>
  ~~~~~~~~~~

We expect ISTC entry to lead to efficiency improvements at nearby incumbents. As mentioned
in Section 1, we measure hospital efficiency using pre-surgery LOS. Prospective
reimbursement systems (like PbR in England) pay hospitals on the basis of outputs rather
than inputs. This creates incentives for hospitals to reduce marginal costs by shortening
patient LOS (Cutler, 1995). Empirical studies of England (Farrar et al., 2009), the United
States (Feder et al., 1987; Guterman and Dobson, 1986; Feinglass and Holloway, 1991; Kahn
et al., 1990), Israel (Shmueli et al., 2002) and Italy (Louis et al., 1999) provide
evidence that prospective reimbursement leads to shorter LOS. While prospective
reimbursement systems provide incentives for all hospitals to reduce patient LOS, these
incentives will likely be particularly sharp in more competitive markets. Hospitals
located in less competitive markets likely have limited scope to expand their activity
because they are constrained by the relative inelasticity of clinical demand within their
catchment areas. By contrast, hospitals in more competitive markets have greater
opportunity to expand activity by capturing market share from other hospitals. To create
capacity for such expansion, in health care systems with prospective reimbursement,
hospitals in more competitive markets are likely to take stronger action to reduce patient
LOS, so that they can treat additional patients. Consistent with this hypothesis, studies
of the 2006 patient choice reforms in the English NHS found that hospitals located in more
competitive markets decreased their LOS by larger amounts than hospitals in less
competitive markets (Cooper et al., 2012; Gaynor et al., 2013). In light of this
theoretical prediction and empirical evidence, we hypothesise that incumbent hospitals
exposed to entry by an ISTC will have reduced patient LOS over and above any secular
decreases in LOS resulting from the introduction of prospective reimbursement. We
therefore identify the effect of ISTC entry on the efficiency of nearby public hospitals
using a DiD estimator in which the treatment effect equals the change in efficiency at
ISTC-exposed public hospitals minus the change in efficiency at unexposed public
hospitals. During the 2000s, the government announced that performing elective surgery on
the day of a patient's admission was a key measure of hospital performance, and
highlighted that ISTCs would be particularly effective at this. The NHS Institute for
Innovation and Improvement (2006, 2008a, 2008b) identified surgery on day of admission as
one of the six characteristics of high-performing orthopaedic surgical facilities and
argued (2006, p.20) that public hospitals would have to respond to competition from
private entrants by streamlining their production: “Same-day admissions [i.e. admission on
day of surgery] are seen as imperative by independent [private] providers. Acute [public]
trusts will need to reflect this as an integral element of any market strategy when
seeking to demonstrate competitive advantage.” This explicit focus on admission on day of
surgery means that, in addition to the more general incentives to increase efficiency
brought about by surgical centre entry, we expect public hospitals facing increased
pressure from private surgical centres to have improved their performance in this
dimension in particular.

<hs>  Case mix</hs>
  ~~~~~~~~

The entry of private, for-profit surgical centres could also change the case mix at nearby
incumbents due to risk selection by entrants. Whereas in classical private goods markets
the profitability of selling to a particular customer is determined solely by their
willingness to pay, in health care markets – as in many other markets for the provision of
public services, such as social care and education – the profitability of treating a given
customer will be influenced by characteristics of the customer that are often imperfectly
observed. The influence of patient characteristics on profitability provides all hospitals
with an incentive to refuse to treat the sickest patients. However, private, for-profit
entrants like ISTCs are likely to be more willing than public hospital incumbents to
actively select against costly patients, as for-profit firms are able to redistribute
profits to shareholders, whereas public hospitals are, at most, only allowed to reinvest
profits into the organisation. The literature on specialty hospitals in the US, for
example, has found evidence that these providers select low-risk patients, leaving the
sickest patients to nearby general hospitals (Barro et al., 2006; Winter, 2003; Cram et
al., 2005). Two further factors add weight to the hypothesis that ISTCs had stronger
incentives to risk-select than public hospital incumbents. First, ISTCs could legally
decline to treat complicated cases, whereas public hospitals were formally prohibited from
doing so. Second, as mentioned previously, ISTCs were prohibited from using NHS doctors,
so their workplace culture likely differed sharply from that at incumbents. As Rose-
Ackerman (1996) notes, the culture of staff plays a key role in dictating firm behaviour –
thus these cultural differences may have led ISTCs to be more willing than NHS providers
to engage in profit-driven risk-selection. Prospective reimbursement encourages cream-
skimming, since it provides incentives for hospitals to avoid admitting patients whose
cost of treatment is likely to exceed the regulated payment (Allen and Gertler, 1991;
Ellis and McGuire, 1986; Ellis, 1998; Newhouse, 1989). We use DiD methods to estimate the
extent to which ISTCs left incumbent NHS hospitals with a sicker, costlier mix of
patients, over and above any secular changes in case mix over this period (either as a
result of the introduction of prospective reimbursement, or for other reasons). Previous
studies have confirmed that ISTCs treated healthier and less complex patients than nearby
public hospitals (Street et al., 2010; Mason et al., 2008, 2010; Browne et al., 2008;
Chard et al., 2011; Fagg et al., 2012). However, no one has yet compared the evolution of
average patient severity at ISTC-exposed public hospitals with that at public hospitals
unaffected by the ISTC programme, and shown that ISTC-exposed public hospitals experienced
a larger reduction in average patient health status (measured using a Charlson Index) than
public hospitals not exposed to the entry of an ISTC. Providing evidence of such an effect
of ISTC entry is important because the case mix differences between ISTCs and nearby
public hospitals documented by the existing literature may simply reflect the fact that
ISTCs attracted patients who would not otherwise have undergone surgery.7

<h>DATA, DEFINITION OF TREATMENT GROUP, AND ESTIMATION STRATEGY</h>
------------------------------------------------------------

Our aim is to estimate the causal effect of the entry of private surgical centres on the
efficiency, case mix, and case load of nearby incumbent public hospitals. We use
difference-in-difference (DiD) regressions in which the impact of ISTC exposure is
estimated from the mean change in outcomes for public hospitals in a treatment group
(those that had a private surgical centre placed nearby) minus the mean change in outcomes
for public hospitals in a control group (those that did not have a private surgical centre
placed nearby) before and after entry occurred. This section describes our outcome
measures, construction of treatment groups, and identification strategy.

<hs>  Data and outcome variables</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~

Our dataset is derived from the NHS Hospital Episode Statistics (HES) (HSCIC, 2016), which
contains the universe of government-funded hospital admissions in England.8 Our data
extract consists of all elective hip and knee replacements on patients aged 55–100
performed between financial years 2002/3 and 2008/9 (see Table 1). We focus on hip and
knee replacements for two reasons. First, orthopaedic surgery was a major focus of the
ISTC programme, as it was recognised in the early 2000s that achieving the government's
waiting time targets was going to be more challenging in this surgical specialty than in
any other area (Harrison and Appleby, 2005). Second, clinical practice in relation to hip
and knee replacements did not change significantly during this period in ways that could
affect LOS. As a result, any observed changes in LOS will likely be driven by NHS reforms,
not by differential uptake of new medical technologies. We focus on hip and knee
replacements performed in NHS hospitals. NHS hospital trusts (firms) often consist of
multiple hospitals (individual sites) that can be located up to 100 km away from each
other. We therefore analyse the data at site (hospital) level rather than trust (firm)
level, and assign hospitals (sites) to treatment and control groups based on the site's
proximity to the nearest ISTC. All references to ‘hospitals’ in this paper are therefore
to hospital sites, not to trusts (firms). After cleaning and imputing missing values for
the site code field, and applying exclusion criteria detailed below, there are 166 public
hospitals treating hip and knee replacement patients from 2002/3 to 2008/9. Researchers
have generally struggled to quantify hospital efficiency. In the absence of hospital cost
data, many studies use proxy measures of efficiency such as LOS (Fenn and Davies, 1990;
Martin and Smith, 1996; Gaynor et al., 2013). The logic underlying this measure is that,
if a hospital can treat patients more quickly without any deterioration in clinical
quality, then it must have become more efficient. However, a critical shortcoming of
overall LOS as an efficiency measure is that recovery time after surgery is also heavily
dependent on patient characteristics and health status. Moreover, a hospital's average LOS
may reflect undesirable hospital behaviour such as cream skimming (prioritising treatment
of less costly patients); dumping (avoiding treatment of costlier patients); and quality
skimping (discharging patients ‘sicker and quicker’) (Epstein et al., 1990; Martin and
Smith, 1996; Sudell et al., 1991). In this study, we use an innovative method to obtain a
cleaner proxy for hospital efficiency. We decompose LOS for hip and knee replacements into
two parts: the time from admission to surgery (pre-surgery LOS), and the time from surgery
until discharge (post-surgery LOS). We hypothesise that, for elective orthopaedic surgery,
pre-surgery LOS is not significantly influenced by patient characteristics, as there is
rarely a clinical rationale for admitting an elective orthopaedic surgery patient before
the scheduled day of their operation. In the early 2000s, fewer than 20% of hip and knee
replacement patients had surgery on the day they were admitted to the hospital. Patients
were often kept overnight before elective surgery not for clinical reasons, but because
operating rooms were not available on their scheduled surgery date.9 The extent to which
hospitals are able to schedule patient admissions to ensure that they line up with the
availability of surgeons, support staff, and operating theatres will therefore be a direct
function of the efficiency with which the hospital is run. By contrast, we view post-
surgery LOS as a joint product of underlying hospital efficiency and patient
characteristics. Therefore, when we estimate the effect of ISTC entry on post-surgery LOS,
we interpret the results as a combined outcome of (i) competitive pressure brought about
by ISTC entry, leading to efficiency improvements by nearby public incumbents, and (ii)
ISTC cream skimming, leaving nearby public hospitals with a sicker mix of patients. To
test our hypothesis that pre-surgery LOS is less influenced by patient characteristics
than post-surgery LOS, we regress pre- and post-surgery LOS for hip and knee replacements
against a range of patient characteristics. Patient characteristics included in the
regression are: Charlson score; number of diagnoses; Index of Multiple Deprivation (IMD)
income deprivation score; IMD health and disability deprivation score; dummy variables
indicating self-discharge, urban residence, mixed ethnicity, Asian ethnicity, black
ethnicity, other ethnicity, and unknown ethnicity; and a full set of case mix dummies with
gender interacted with five-year age bins. The results, reported in Table 2, are
consistent with our hypothesis – patient characteristics explain less than half a per cent
of the variation in pre-surgery LOS, but 12.8% of the variation in post-surgery LOS. We
observe changes in patient health status at NHS hospitals before and after ISTCs enter in
order to directly measure whether risk selection occurred. To measure patient health
status, we calculate a Charlson score for each patient. The Charlson score predicts a
patient's 10-year survival probability based on their health status in relation to 17
conditions likely to lead to death. The score varies from 0 to 6, with 0 denoting the
absence of any predictors of mortality (HSCIC, 2013).10 As proxies for health status and
clinical risk, we also use the patient's age, as well as the IMD income domain (Noble et
al., 2004), which reports the percentage of households in the patient's residential Lower
Super Output Area (LSOA, a statistical geographical areas containing around 1500
residents) that are income deprived (in our dataset this variable ranges from 0 to 83).
The data includes 478,226 hip and knee replacements performed from 2002/3 to 2008/9 that
met the sample restrictions. As Table 1 illustrates, during the analysis period pre-
surgery LOS, post-surgery LOS, and total LOS fell considerably.11

<hs>  Treatment assignment</hs>
  ~~~~~~~~~~~~~~~~~~~~

We assign public hospitals to treatment or control groups based on their geographical
proximity to the new market entrants, on the assumption that exposure to competition from
these entrants is a product of proximity. In particular, we assign treatments by comparing
the distance from an NHS hospital to its nearest ISTC with the percentiles of distance
travelled by that hospital's hip and knee replacement patients. We measure the distance
travelled by each hip and knee replacement patient to hospital using the centroids of a
patient's residential LSOA to define home location. We then calculate, for each NHS
hospital, percentiles of patient distance travelled (e.g. the distance that captures 25%
of a hospital's hip and knee replacement patients). Percentiles of patient distance
travelled can be endogenous to hospital quality – for example, a high-quality hospital may
attract patients from further afield. To ameliorate this concern, we use percentiles of
patient distance travelled based on patient flows from 2002/3 to 2004/5 (i.e. before
implementation of either the ISTC programme or patient choice of hospital for elective
surgery). Table 3 presents descriptive statistics for quantiles of patient distance
travelled and the exposure of NHS hospitals to Wave 1 ISTCs within each of these quantile
bands. Panel A presents the mean kilometre distances (averaging over the NHS hospitals in
our estimation sample) corresponding to these patient percentile travel distances. The
mean value of the 25th percentile of travel distance for hip and knee replacement patients
is 4.25 km, while for the 95th percentile it is 26.34 km. Panel B shows how many NHS
hospitals had a Wave 1 ISTC enter within each of these distance bands. To define Treatment
and Control groups, we start by assuming that, if there is no ISTC entrant within an NHS
hospital's 95th percentile of patient distance travelled – a widely-used definition of
market size – then the NHS hospital is not exposed to the ISTC programme. These NHS
hospitals are assigned to the Control group. We assign the remaining NHS hospitals to
discrete treatment groups based on natural breaks in the distribution of distances from
NHS hospital to the nearest ISTC in our dataset, measured in terms of patient travel
percentiles (see Fig. 2). This assignment yields two discrete treatment groups – a Low
Treatment group (ISTC within 95th percentile of patient distance travelled but not within
25th percentile) and a High Treatment group (ISTC within 25th percentile of patient
distance travelled).12 There are 11 NHS hospitals in the High Treatment group, 51 in the
Low Treatment group and 104 in the Control group. Fig. 3 maps the ISTCs and public
hospitals in our data. In the robustness section, we show the effect of changing the
threshold used to define the treatment groups on our estimates. One obvious concern is
that treatment assignment might be endogenous to our primary outcome (LOS) because ISTCs
may have opened near inefficient NHS providers. However, as noted earlier, ISTC placement
decisions were driven by local NHS hospital waiting times, not by local hospital LOS or
other performance measures. Waiting times are dependent on a wide range of demand and
supply side capacity-related factors beyond simply hospitals' LOS. As a result, there is
little reason to expect hospitals with high waiting times to necessarily have high LOS.
Indeed, as we observe, hospitals' LOS is uncorrelated with their waiting times.13 Table 4
illustrates this point by comparing waiting times, total LOS, pre-surgery LOS, and post-
surgery LOS for hip and knee replacement at High Treatment group, Low Treatment group and
Control group hospitals in 2002/3 (the year that ISTC placement decisions were being
made). Average waiting times in 2002/3 were around 6% higher at High Treatment group
hospitals than at hospitals in our other groups. By contrast, there are no systematic
differences between total LOS or post-surgery LOS at High Treatment group hospitals and
others. Pre-surgery LOS is slightly lower at High Treatment group hospitals – i.e. ISTCs
tended to enter near NHS hospitals that were already slightly more efficient, although
there is no evidence to suggest that these small efficiency differences were a factor in
ISTC location decisions. As we show in later analysis, these differences in pre-surgery
LOS are not associated with any statistically significant differences in trends of pre-
surgery between 2002/3 and 2004/5, prior to the entry of ISTCs – which is the key
assumption of our DiD identification strategy. The fact that ISTCs entered where nearby
public hospitals were already more efficient might be of concern if we were to find that
ISTC exposure led nearby public hospitals to become less efficient, as it might suggest
that mean reversion is driving our results. However, as we find the opposite (i.e. ISTCs
entered near public hospitals that were already more efficient, and that became even more
efficient in relative terms as a result of ISTC exposure), we have no reason to be
concerned that these small differences in pre-ISTC levels of pre-surgery LOS across
treated and control groups will confound our DiD estimates. We allocate NHS hospitals to
treatment categories by comparing distance to ISTC with percentiles of patient distance
travelled, not with kilometre distances, to control for rural-urban differences –
treatment assignment based on fixed distances will over-estimate the size of markets in
urban areas relative to rural areas, given the impact of urban congestion on travel
speeds. In the robustness tests, we examine whether our results change if we use a
treatment assignment strategy based on fixed distances from public hospital to ISTC.

<hs>  Treatment start and end dates</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

There is some ambiguity as to the appropriate way to define the policy-on and policy-off
dates for a given public hospital exposed to ISTC entry. As the first ISTCs in our
analysis opened in April 2005 (financial year 2005/6), we define 2004/5 as the last pre-
treatment (pre-ISTC-programme) financial year.14 However, some ISTCs did not begin
operations until 6 months to a year after their contracted start date. Moreover, when the
initial ISTC contracts (generally around 4 or 5 years in length) were completed, some
managed to secure further contracts, but others were shut down or absorbed into
neighbouring NHS trusts. The fate of an ISTC was generally announced in the last year of
the contract. Thus, if contract end date were used as treatment end date, estimates of
treatment effects could be confounded by changes in behaviour due to anticipated contract
completion. In response to these ambiguities, we employ a long differences specification
using data from the 2004/5 and 2008/9 financial years. We choose 2004/5 as the pre-
treatment period in our main specification because it is the last year before the first
contract start date amongst the ISTCs we use for treatment assignment, and thus most
likely to capture the effect of ISTC exposure as distinct from the effect of other
elements of the government's reform programme. We choose 2008/9 as the post-treatment
period to allow time for treatment effects to be realised, while avoiding contamination
from responses to announcements concerning extension or non-extension of ISTC contracts.
For robustness, we show how treatment effects change annually in the post-reform years
from 2005/6 to 2008/9, and report estimates that define a public hospital's treatment
start date as the contract start date of its nearest ISTC.

<hs>  Regression specification</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~

We identify the impact of hospital market entry using a DiD regression framework where
dummy variables indicating treatment group membership are interacted with a post-policy
dummy, which is switched on for the 2008/9 financial year. Regressions are run at the
patient level and any non-binary dependent variables are log-transformed (after adding 1
to any variables that have a minimum value of zero) such that the treatment effects are
interpretable as percentage changes. In this specification, t denotes the time period
(financial year), postt ∈ {0, 1} denotes whether an observation occurs in the post-reform
period, yijt denotes the outcome variable under consideration for patient i attending
hospital j at time t, and highj and lowj denote dummies for the High and Low Treatment
groups respectively. Treatment effects are given by the coefficients on the interaction
terms, β4 and β5. We also include a dummy in our regressions to control for the type of
procedure a patient undergoes (hip or knee surgery) but suppress this in the notation for
simplicity. Our third specification is identical to (2), but includes an extensive set of
controls for patient and hospital characteristics.15 All specifications are estimated
using ordinary least squares (OLS), with standard errors clustered at the hospital level
to account for correlation in unobservables within hospitals (between patients and over
time). There are two core threats to our identification strategy. The first is that trends
in outcome variables may not have been parallel between treatment and control groups prior
to ISTC entry. The second is that there may have been other time-varying policy changes
that also affected outcomes concurrently with the ISTC programme. To address the first
possibility, we demonstrate that treated and control hospitals had parallel trends for our
key dependent variables before the ISTC programme was launched by showing trends in the
data graphically, and formally testing for statistically significant differences in
trends. To address the risk that concurrent and correlated policy shocks drive our
results, Section 5.4 discusses the two most prominent policy changes that could have
affected outcomes contemporaneously with ISTC entry – the introduction of hospital
competition via patient choice of hospital for elective surgery, and the enactment of
differential health policies by Strategic Health Authorities (SHAs) – and illustrates that
controlling for these policy changes does not materially influence our main estimates.

<hs>  Descriptive evidence</hs>
  ~~~~~~~~~~~~~~~~~~~~

Fig. 4 presents the evolution of key outcome variables – pre-surgery LOS, percentage
treated on day of admission, post-surgery LOS, total LOS and Charlson score – between
2002/3 and 2008/9, for treatment and control groups. The shaded area represents the range
of treatment start dates for the Wave 1 ISTCs. We expect that any treatment effects will
arise either within the time period captured by shaded region or, if behavioural responses
took place with a lag, some time thereafter. Each data point represents a month, but the
plots are smoothed using a moving average of the month and the previous quarter. These
graphs allow visual examination of whether treated and control groups followed similar
trends prior to the entry of ISTCs. Panel A shows changes in pre-surgery LOS and
illustrates that High Treatment group, Low Treatment group, and Control group hospitals
follow similar trends before ISTC entry. Over and above a secular downward trend,
reflecting general improvements in turnaround time, there is evidence of a treatment
effect from ISTC entry. After ISTC entry, trends diverge, and by the end of the treatment
period the reduction in pre-surgery LOS is notably larger for the High Treatment group
than for the Control group. There also appears to be a smaller effect for the Low
Treatment group. Panel B shows trends in the percentage of patients treated on the day of
admission. All three groups have similar pre-entry trends, but after ISTC entry the
percentage of patients treated on the day of admission increases more quickly for High
Treatment group hospitals. Overall, Panels A and B provide visual evidence that the entry
of private specialty surgical centres in the English NHS made nearby public hospitals more
efficient, by reducing pre-surgery delays. Panel C shows trends in post-surgery LOS, which
have a markedly different pattern. The High Treatment group, Low Treatment group, and
Control group hospitals have similar pre-entry trends. However, there is a sharp increase
in post-surgery LOS for the High Treatment group from the middle of the ISTC entry period
onwards. Overall, after ISTC entry post-surgery LOS decreases in the High Treatment group
less than in the Control group. Panel D presents trends in total LOS, which follow a
similar pattern to post-surgery LOS. As discussed in Section 4.1, post-surgery LOS (and
therefore total LOS) will be influenced both by changes in hospital efficiency due to
increased competitive pressure from the entry of private surgical centres, and by changes
in patient characteristics due to cream skimming by entrants. Panels C and D therefore
provide suggestive evidence that the negative impact of ISTC cream skimming on nearby
public hospitals' LOS may have outweighed any efficiency improvements with respect to LOS
arising from competitive pressure from these new market entrants. Panel E looks more
directly at the impacts of ISTC entry on public hospitals' case mix by plotting the
evolution of average Charlson scores. The pre-policy levels and trends of the Charlson
score are similar across treatment and control groups. However, the High Treatment group
starts receiving sicker patients from early in the ISTC entry period. This evidence is
consistent with our hypothesis that selection of less risky patients by ISTCs left a
residual pool of higher-risk patients to be treated by public hospitals. Graphical
evidence for other case mix variables is presented Appendix D. Overall, the similar pre-
policy trends in treatment and control groups for all outcome variables provides strong
support for our argument that DiD estimates are likely to provide an unbiased estimate of
treatment effects from ISTC entry. The fact that pre-policy trends (and in many cases
levels) of our outcome variables are similar across treated and untreated groups is
consistent with our argument that the principal target of ISTC placement was to reduce
waiting times for admission to hospital, not to reduce time spent in hospital or to
improve clinical quality.16

<hs>  Regression-based difference-in-difference estimates</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Table 5 presents our main difference-in-difference estimates of the effect of ISTC entry
on log of pre-surgery LOS, percentage of patients treated on day of admission, and log of
post-surgery LOS. The sample includes hip and knee replacements, with a hip replacement
dummy included to account for level differences in outcomes between the two procedures. In
Columns (1) to (3), the dependent variable is log of pre-surgery LOS. Column (1) presents
estimates of Eq. (1), without hospital fixed effects or patient controls. The estimate
implies that ISTC entry led to a 14.4% (=100(e−0.156 − 1)) reduction in pre-surgery LOS.
In Column (2), we estimate Eq. (2), adding hospital and month × year fixed effects. The
results are qualitatively unchanged and imply that ISTC entry led to a 16.1% reduction in
pre-surgery LOS. In Column (3), we add patient controls and the results again remain
qualitatively unchanged (we find a 16.6% reduction). That controlling for patient
characteristics barely shifts the estimated treatment effects for the High Treatment group
suggests that there is little selection into treatment on the basis of these observable
demographic characteristics. This, in turn, implies that there is likely to be little
selection into treatment on the basis of unobservable patient characteristics (Altonji et
al., 2005). The impact on the Low Treatment group is of the same sign and around one third
the magnitude of the High Treatment group effect, but is imprecisely measured and never
significant at conventional levels. The most likely interpretation is that there were
moderate impacts of ISTC entry on the Low Treatment group, but that our research design
does not have sufficient power to detect them. Columns (4) to (6) examine the effect of
ISTC entry on the proportion of patients who were treated on the day of admission. The
results are similar with and without hospital fixed effects, and with and without patient
controls. The results in Column (5), which estimates Eq. (2), shows that ISTC entry led to
a 24.3 percentage point reduction in the proportion of patients treated on the day of
admission at High Treatment group hospitals, from a baseline of 22.8% in 2004/5. As with
pre-surgery LOS, the impact on the Low Treatment group is same-signed, smaller, and never
significant at conventional levels. Columns (7) to (9) present estimates of the effect of
ISTC entry on post-surgery LOS. In Column (7), we estimate that the entry of ISTCs led to
an 8.47% increase in post-surgery LOS at High Treatment group hospitals. However, this
effect is only significant at the 10% level. The precision and magnitude of our estimates
is reduced when hospital and month × year fixed effects are included, in Column (8).
Adding patient controls further reduces the size of the point estimate and decreases
precision, as we would expect if patient characteristics affect post-surgery LOS and it is
selection of less riskier patients into ISTCs and out of NHS hospitals which drives the
treatment effects on post-surgery LOS. That patient controls reduce the magnitude of the
post-surgery LOS estimates, but have little impact on the pre-surgery LOS estimates,
provides further evidence that patient characteristics are a major driver of post-surgery
LOS, but have little influence on pre-surgery LOS. We interpret changes in post-surgery
LOS resulting from ISTC entry as a joint product of (i) changes in the mix of patients
being treated by public hospitals, due to cream skimming by neighbouring ISTCs and (ii)
behavioural responses by public hospital managers and clinicians to competition from new
private entrants. Although only significant at the 10% level, the estimates in Column (7)
suggest that the increases in post-surgery LOS generated by cream-skimming were larger
than the reduction in LOS generated from any efficiency gains in terms of the total time
patients spent in the hospital. An important point to note, in relation to the results
presented in Table 5, is that the unreported coefficients on the High Treatment and Low
Treatment indicators in Columns (1), (4) and (7) are always near-zero and statistically
insignificant. For example, in Column (1) the coefficient on the High Treatment variable
is 0.0308 (0.0442). These results imply that the treatment and control groups are balanced
in terms of the pre-treatment, 2004/5 levels of the outcomes under investigation,
consistent with the graphical evidence in Fig. 4 discussed above.17 Table 6 tests for
cream skimming directly by assessing whether the entry of an ISTC left nearby public
hospitals with a riskier mix of patients. We estimate Eq. (1) and Eq. (2) with hospital
and month × year fixed effects; no specifications include patient controls. Columns (1) to
(4) indicate that ISTC entry led to an 11.6% increase in the average Charlson score of
patients at High Treatment group hospitals – or a 6.2 percentage point increase in the
proportion of patients with a Charlson score of three or more – significant at the 5%
level. Column (5) indicates that ISTC entry led to a 5.54% increase in the IMD income
deprivation score at High Treatment group hospitals, although this point estimate reduces
in magnitude and becomes imprecise when hospital and month × year fixed effects are added.
We do not find that ISTC entry led to a precisely estimated increase in patient age at
nearby NHS hospitals. Table 7 presents event study estimates of year-by-year effects of
ISTC entry on log of pre-surgery LOS, percentage of patients treated on day of admission,
and log of Charlson score at exposed NHS hospitals, from 2004/5 to 2008/9. The estimates
mirror our graphical evidence in Fig. 4 and show that ISTC entry had a statistically
significant effect on these outcomes at exposed NHS hospitals from 2007/8 onwards.
Appendix J explores the impact of ISTC entry on clinical quality at NHS hospitals by
analysing changes in 30-day in-hospital mortality from acute myocardial infarction (AMI)
at nearby public hospitals. We find that, after controlling for patient characteristics,
ISTC entry did not have a statistically significant effect on AMI mortality at nearby
public hospitals. The results suggest that the efficiency improvements reported in Columns
(1) to (6) of Table 5 were achieved without any evidence of concomitant deterioration in
clinical quality.

<hs>  Treatment assignment using fixed distances</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Table 8 presents estimates of the effect of ISTC entry when treatment assignment is based
not on patient flows but on fixed kilometre distances between ISTCs and NHS hospitals.
Specifically, the High Treatment group comprises NHS hospitals that had an ISTC enter
within 5 km, the Low Treatment group comprises NHS hospitals that had an ISTC enter within
30 km (but not within 5 km), and the Control group comprises NHS hospitals that did not
have an ISTC enter within 30 km. Using this definition, the High Treatment group contains
14 hospitals, the Low Treatment group 78 hospitals, and the Control group 77 hospitals.
Table 8 indicates that ISTC entry within 5 km of an NHS hospital led to a 14.7% reduction
in pre-surgery LOS, a 21.9 percentage point increase in the share of patients treated on
the day of admission, and an 11.2% increase in the average Charlson score.

<hs>  Controlling for contemporaneous NHS policy changes</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

One concern with our DiD identification strategy is that the resulting estimates may be
biased by other policies, implemented concurrently with the ISTC programme, that had a
differential effect on our outcome variables across treated and control groups. The most
prominent such policy is the 2006 introduction of hospital competition within the NHS via
patient choice of hospital for elective surgery. In addition, during this era much NHS
policy was dictated by ten regional Strategic Health Authorities (SHAs) – differences in
SHA policies implemented during the ISTC period may bias our results, to the extent that
ISTC entry was differentiated across regions of England. We investigate these
possibilities in Table 9; all reported estimates use as their baseline Eq. (2). Columns
(1) to (3) test whether the estimates reported in Tables 5 and 6 are robust to controlling
for the 2006 patient choice reforms. We control for overall competition intensity by
including a measure of market concentration (a time-invariant negative log of hospital
HHI) interacted with a post-ISTC-entry dummy variable.18 If the patient choice reforms
were driving the results, inclusion of this interaction term would severely attenuate our
estimates. However, including this interaction term does not materially change the
estimates – they remain precisely estimated and similar in magnitude. Columns (4) to (6)
test for other region-specific policy changes that could be driving our results. To do so,
we interact dummies for each of the ten English SHAs with a post-ISTC-entry dummy. These
additional controls do not materially impact our results. The results are also robust to
controlling more flexibly for differential SHA policies and regional trends via separate
SHA × year or SHA × year × month interaction terms (see Appendix G). Overall, the
estimates reported in Table 9 provide assurance that our main estimates are not driven by
the most worrisome potential sources of bias from contemporaneous policy changes.

<hs>  Altering the threshold used to define treatment exposure</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

So far, we have defined the High Treatment group to include any public hospital that had
an ISTC enter within the 25th percentile of patient distance travelled between 2002/3 and
2004/5, or, in the alternative specification reported in Table 8, within 5 km. Figs. 5 and
6 show how the estimates of Eq. (2) change as we vary the treatment group definition
thresholds. Fig. 5 (Panel A for log of pre-surgery LOS and Panel B for log of Charlson
score) shows how the estimates change when the threshold used to define the treatment
group changes from one that captures 15% of a hospital's hip and knee replacement
patients, to one that captures 95%. Panels A and B illustrate that the estimated treatment
effects decrease as the treated group is defined more widely. Fig. 6 performs the same
exercise when defining treatment exposure using fixed distances from NHS hospital to ISTC,
as in Table 8. Panel A shows that ISTC entry within 5 km of an NHS hospital leads to a
precisely estimated reduction in log of pre-surgery LOS at incumbents. As the threshold
used to define the treatment group increases, the estimated treatment effects lose
precision and asymptote to zero. Panel B, for log of Charlson score, shows a similar
sensitivity to the threshold used to define treatment exposure. ISTC entry within 5 km of
an NHS hospital leads to a large and statistically significant increase in the average
Charlson score at incumbents, with estimated treatment effects decreasing as the distance
to ISTC used to define the treatment group increases. Overall, Figs. 5 and 6 demonstrate
that our estimated treatment effects are robust to the exact threshold used to define
treatment exposure. Furthermore, as the treatment group is expanded, there is a negative
gradient to our estimates, which is broadly supportive of the argument that our estimated
treatment effects are driven by ISTC exposure.

<hs>  Additional tests of robustness</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Table 10 reports additional robustness tests for our main estimates of the impact of ISTC
entry on log of pre-surgery LOS, percentage of patients treated on day of admission, and
log of Charlson score at High Treatment group hospitals. We estimate Eq. (2) unless
otherwise noted. Panel A formally tests for parallel pre-reform trends for the High
Treatment group relative to the Control group using a ‘placebo’ DiD regression where
2002/3 is the base year and 2004/5 (the last year before ISTC entry) is the treated year.
This regression allows us to explore whether there was a statistically significant
difference in the change in key outcomes in our High Treatment group relative to the
change in key outcomes for the Control group during our pre-period from 2002/3 to 2004/5.
If there were statistically significant differences (i.e. a ‘placebo’ treatment effect),
it would illustrate that there was a difference in trends over the pre-reform period that
would potentially invalidate our identification strategy. Consistent with the graphical
evidence in Fig. 4, none of the 2002/3 to 2004/5 point estimates are statistically
significant at conventional levels, confirming that there were no statistically
significance differences in trends for key outcomes between our control group and high
treatment group from 2002/3 to 2004/5 (our pre-period). Though not reported, we also find
no statistically significant treatment effects for the Low Treatment group relative to the
Control group over the same period. To address any residual concerns about comparability
of treated and untreated hospitals, Panel B reports inverse propensity score weighted
estimates where we weight our treatment and control groups by the inverse of the
probability that an observation belongs in its group. To do this, we first calculate the
probability of a hospital being assigned to the High and Low Treatment groups based on
hospital and average patient characteristics.19 We then run separate regressions to
estimate treatment effects for the High and Low Treatment groups, using as probability
weights the inverse of the probability of assignment to the group that the observation was
actually assigned to. While it is impossible to reject a null hypothesis of no significant
differences between treated and control groups with respect to the above determinants of
treatment assignment even before these weights are applied, weighting by the inverse
propensity score increases the similarity of the treated and control groups further still,
by giving higher weight to control observations that look more like treated observations,
and vice versa. The resulting estimates are similar to the headline findings, but more
precise. The corresponding (unreported) estimates for the Low Treatment group are not
statistically significant. Our main specification accounts for the fact that different
ISTCs commenced operations at different times by using a long differences estimation
strategy with 2004/5 as the pre-reform year and 2008/9 as the post-reform year. An
alternative approach is to define t = 0 (the treatment start date) for each public
hospital as the contract start month (or month of ‘full service commencement’) of the
nearest ISTC, and to use pre- and post-reform periods defined relative to t = 0 rather
than using calendar time. We do not use this as our main specification because the
contract start date is not always an accurate indicator of when an ISTC started treating
patients. Nonetheless, Panel C presents estimates from such a specification, with months
−12 to −1 before ISTC entry designated as the pre-reform period, and months 24 to 35 after
entry designated as the post-reform period. Hospitals in the Control group are allocated a
placebo ‘treatment’ start date equal to the contract start date of the nearest ISTC, even
though this ISTC lies outside the 95th percentile of patient distance travelled. The
resulting estimates are very similar to our main results. Panel D reports estimates using
a treatment assignment strategy that centres hospital markets on GP surgeries rather than
hospitals. Hospital-centred measures of market size based on percentiles of patient
distance travelled are potentially endogenous to hospital performance. While we address
this concern by basing treatment assignment on percentiles of patient distance travelled
between 2002/3 and 2004/5 – before the introduction of patient choice of hospital or the
ISTC programme – concerns may remain. To address these concerns, this check assigns
treatments by constructing a list of all the NHS hospitals and ISTCs that fall within each
GP surgery's market (95th percentile of distance from GP surgery to NHS hospital for that
GP surgery's hip and knee replacement patients). If an ISTC is in 95% of the GP surgery
markets that an NHS hospital falls within, that NHS hospital is assigned to the High
Treatment group. If an ISTC is in 75% of the GP surgery markets that an NHS hospital falls
within, but not 95%, that NHS hospital is assigned to the Low Treatment group. All other
NHS hospitals are assigned to the Control group. The estimates reported in Panel D are
consistent with our main results, providing assurance that they are not driven by
assignment of treatments based on hospital-centred market definitions. Panel E reports
estimates when we do not take logs of the outcome variables (pre-surgery LOS and Charlson
score). We continue to find that ISTC entry made nearby public hospitals more efficient,
but also left them with sicker patients; the estimates are nearly equal to the exponent of
our main results. A number of other checks are reported in the online Supplementary
Material (see Appendices E through G); they provide further confirmation that our results
are robust to a wide range of specifications.

<hs>  Ruling out the possible confounding effect of changes in patient volumes</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Increases in local capacity could potentially affect incumbents' efficiency by reducing
congestion and overcrowding, independent of any competitive pressure exerted by entrants.
Moreover, public hospitals located near new private entrants may have experienced a
reduction in demand. Any resulting reduction in case loads at nearby public hospitals
could affect average pre-surgery LOS at these incumbents, given the important influence of
volume on efficiency. We therefore investigated the impact of ISTC exposure on case load
using similar regressions to those used for our main estimates, but found no statistically
significant evidence of case load reductions in our High Treatment group, which had the
biggest reductions in pre-surgery LOS (results available in Table H.1 in the online
Supplementary Material). This suggests that the increases in local capacity brought about
by private surgical centre entry did not lead to any reduction in the volume of patients
treated at High Treatment group hospitals, but, instead, served to take people off waiting
lists and reduce waiting times. That is, ISTC exposure led to shorter pre-surgery LOS in
close-neighbouring hospitals without any concomitant reduction in the volume of patients
being treated. We did find, however, significant reductions in the volume of patients
being treated at Low Treatment group hospitals. This finding seems to suggest that ISTC
entry did not simply add to overall clinical capacity, but, at least to some extent, may
have reduced patient volume at public hospitals with which they shared a market –
although, crucially, these patients seem not to have been drawn from the closest hospitals
(i.e. those in the High Treatment group) in which we observe statistically significant
reductions in pre-surgery LOS. These findings are broadly supportive of our conjecture
that the reductions in pre-surgery LOS reported in Table 5 arose primarily through
competitive incentives.20

<h>DISCUSSION AND CONCLUSIONS</h>
--------------------------

This paper examines the effect of a UK government programme designed to increase capacity
and competition by facilitating the entry of private, for-profit specialty surgical
centres into the English NHS. We test the impact that the entry of these facilities –
ISTCs – had on incumbent public hospitals' efficiency, case mix, and case load. We exploit
the fact that ISTC location decisions were driven by local waiting times, not by other
hospital characteristics such as LOS or clinical performance, to construct treatment and
control groups that are comparable with respect to the outcome variables examined. Indeed,
we demonstrate that trends of key outcome variables – including pre-surgery LOS, post-
surgery LOS, and patient case mix – were the same for public hospitals that had an ISTC
enter nearby as for those that did not. We find that public hospitals that had a private,
for-profit surgical centre enter close by experienced substantial reductions in pre-
surgery length of stay for hip and knee replacement surgery. The addition of an ISTC to a
public hospital's immediate neighbourhood led to a decrease in pre-surgery LOS of around
16% – or a 24 percentage point increase in the proportion of patients treated on the day
of admission. Given that these faster turnaround times were achieved without additional
expenditure (as they occurred in an environment with fixed payments per procedure), they
suggest that hospitals exposed to competition from new private entrants became more
efficient. As well as investigating possible positive effects of ISTC entry on the
efficiency of incumbent public hospitals, we looked for evidence of possible negative
effects in the form of worsened case mix. We find that ISTC entry led nearby public
hospitals to experience an 11.6% increase in patients' average illness severity as
captured by the Charlson score – or a 6.2 percentage point increase in the proportion of
patients with a Charlson score of three or more. We also find suggestive evidence that
this increase in the sickness of incumbent hospitals' patients led to an increase in post-
surgery LOS. While our identification strategy is unable to pinpoint how much of this
increase in patient complexity at incumbent NHS hospitals is due to ISTCs actively
applying their exclusion criteria – as opposed, for example, to differential choice
behaviour by sick and healthy patients – the fact remains that surgical centre entry
appears to have led to worsened case mix at nearby incumbents, irrespective of the exact
channel by which this effect arose. In principle, this sorting of patients between private
surgical centres and public hospitals could represent an efficiency-improving division of
responsibility between routine and more complex cases. Indeed, this appears to have been
the government's rationale for including wide-ranging exclusion criteria in ISTC
contracts, which would allow these private entrants to focus on routine cases. Thus, the
risk-selection we document was to some extent an intended policy outcome. However, the
fact that policymakers explicitly intended such a division of responsibility between
private entrants and public incumbents does not automatically imply that the division was
devoid of negative consequences. To ensure that a division of responsibility between
complex and straightforward cases does not have a negative effect on the financial
position of providers that receive the most complex patients, hospitals that treat sicker
patients must be appropriately compensated.21 Unfortunately, NHS reimbursement rates
during the period we study did not adequately adjust for patient severity (Mason et al.,
2008). This situation not only provided private surgical centre entrants with an added
impetus to risk select, but it also meant that nearby incumbent public hospitals were left
treating a costlier mix of patients without adequate financial compensation. While the
prospective reimbursement regime (Payment by Results) was updated in April 2009 to include
a more dramatic adjustment for patient severity, Mason et al. (2008) state that providers
were still likely underpaid for treating sicker patients, and note that is unlikely that a
prospective reimbursement system can ever be designed to fully compensate hospitals for a
more costly case mix. Our work highlights one trade-off that arises from the entry of for-
profit surgical centres. We show that entry can stimulate improvements in the performance
of incumbents, but that entrants may engage in risk selection at the expense of
incumbents. These findings offer insights into many situations involving provision of
public services where profitability is influenced by characteristics of the recipient:
namely that the case for increased private sector involvement should depend, in part, on
comparison of the benefits of increased competitive pressure, with the costs arising from
cream skimming by private entrants. Our work is part of the broader task of evaluating the
overall social welfare implications of the entry of private firms into the market for
delivery of public services. Such an overall evaluation would not only consider the
impacts of private provider entry on the performance of public incumbents, but would also
compare the performance of private and public providers, as well as taking into account
any increases in overall capacity resulting from private surgical centre entry. An
interesting thought experiment is to consider whether our selection results were a
function of the for-profit status of entrants, or of the fact that entrants were
specialist surgical centres who competed against full service hospitals. Ultimately,
theory and the broader evidence suggest that both distinctions – competition from for-
profit ventures and competition from specialist surgical centres – likely drove our
selection results (Barro et al., 2006; Dafny, 2005; Cram et al., 2005; Street et al.,
2010). Our findings raise a key question: is it possible to reap the positive effects of
increased competition resulting from expanded independent sector provision within the NHS,
without the negative effects? It is likely that the answer to this question depends on
whether it is possible to risk-adjust payments and outcome measures sufficiently to ensure
that independent sector providers have an incentive to make profits by raising efficiency
and clinical quality, not by selecting against certain patients. Absent suitably risk-
adjusted payments, new entrants may take steps to attract patients that are less costly to
treat, leaving incumbents with a riskier mix of patients.


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<ART>Dynamic aid allocation
======================

Authors: Patrick Carter, Fabien Postel-Vinay, Jonathan Temple
DOI: 10.1016/j.jinteco.2014.11.005
Year: 2015  |  Pages: 291-304
ASJC codes: 2002, 2003
Keywords: Aid allocation, Foreign aid, Global redistribution

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper introduces a framework for studying the optimal dynamic allocation of foreign aid among multiple recipients. We pose the problem as one of weighted global welfare maximization. A donor in the North chooses an optimal path for international transfers, anticipating that consumption and investment decisions will be made by optimizing households in the South, and accounting for limits in the extent to which recipients can effectively absorb aid. We present quantitative results on optimal aid policy by applying our approach to a neoclassical growth model, where the scope for aid-funded growth is determined by the recipients' distance from steady-state.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Since the 1969 Pearson Commission, there has been a standard benchmark for the generosity
of foreign aid programs: developed countries should donate at least seven-tenths of one
per cent of their GDP. In practice, however, relatively few countries have achieved this
level of generosity. Moreover, its foundations are easy to question. The target was
calculated more than forty years ago using a combination of the Harrod–Domar model and
financial programming. This rather mechanical approach would not command much support
today. In this paper, we introduce a new framework for studying optimal aid policies. We
model foreign aid as a form of global redistribution. A utilitarian, forward-looking
social planner seeks to maximize a weighted average of welfare in the global North and the
global South. The planner decides on an optimal path of international transfers,
anticipating that consumption and investment decisions in the North and South will be made
by optimizing households within each region. These households cannot borrow or lend
internationally, and the scope for global redistribution is limited by diminishing returns
to aid. This framework can be used to study the optimal generosity of aid, and its
relationship to absorptive capacity. It can also be used to inform the timing of aid, and
its allocation across countries that differ in development levels. We describe
circumstances in which donors should seek to increase generosity over time, and examine
whether middle-income countries should ever be a priority for aid. Importantly, the
framework is tractable and could be extended in many directions; for example, it could be
adapted to study the implications of capital mobility for optimal aid policies. The
starting point is to model both the global North and South as neoclassical Ramsey
economies. These economies differ in their levels of TFP and income, and in their
distances from steady-state. Obstfeld (1999) analyzed the effect of exogenous transfers on
a Southern economy; in this paper, that problem will be nested within the problem facing a
Northern donor, so that the level and timing of transfers will be endogenously determined.
At first glance, the Ramsey model may seem too stylized for this purpose, since it
neglects political economy forces that will often be central to aid effectiveness. But the
Ramsey model casts sharp light on a direct consequence of aid flows, which is to relax
intertemporal resource constraints. Studying this in isolation should enhance our
understanding of the choices facing donors. A further motivation is the growing interest
in cash transfers to households as a form of poverty alleviation. Hanlon et al. (2010)
argue that transfers direct to households would be more beneficial than more traditional
forms of aid. In 2013, the Indian government launched an ambitious Direct Benefit Transfer
scheme, intended eventually to replace multiple welfare programs with cash transfers to
households. Using evidence from randomized trials, Gertler et al. (2012) and Haushofer and
Shapiro (2013) find that cash transfers to poor households are partly invested. It is
therefore interesting to ask: what happens when aid is used to relax household budget
constraints, and what are the implications for optimal aid policies? In our framework,
utility functions are concave and some global redistribution is optimal, but its extent
will be constrained by diminishing returns to aid. Obstfeld (1999) concluded that the
welfare benefit of (exogenous) aid was modest even without an aid absorption constraint,
but our analysis turns that logic on its head. If the donor is also seen as a Ramsey
economy, the opportunity cost of aid for the donor is similarly modest. Hence, we
sometimes find that donors should be generous, especially for recipient economies that are
close to subsistence. The welfare impact of aid may be substantial, and aid can be
justified even when a substantial fraction of it is wasted. To investigate the
quantitative implications, we use simulations. Donor and recipient initial conditions are
based on data from the Penn World Table, combined with assumptions on structural
parameters. We consider isoelastic (CRRA) preferences and Stone–Geary ‘subsistence
consumption’ preferences. Under Stone-Geary preferences, the effects of aid on investment
and growth are especially strong, and the donor maintains a higher level of aid generosity
for a longer period. The limits to recipient absorptive capacity play an important role
throughout. When recipients are capable of absorbing relatively high levels of aid, the
optimal path of aid is typically front-loaded. But if the South lacks absorptive capacity,
the North may want to increase the generosity of its aid over time, relative to Northern
GDP. This reflects our assumption that, as the South develops, it can use aid more
effectively. We examine what happens if the donor nevertheless maintains aid as a fixed
share of its GDP, as in the Pearson Commission benchmark, and compare this to the fully-
flexible optimal path. We show that, perhaps surprisingly, the welfare costs of
restricting aid to a fixed proportion of donor GDP are often borne in equilibrium by the
North, rather than the South. Another issue of recent interest has been whether donors
should make transfers to middle-income countries (see, for example, Kanbur and Sumner,
2012). We therefore study what happens in the case of two aid recipients, where one is a
low-income country and one a middle-income country with a larger population. Our
simulations of optimal policies indicate large changes over time in aid generosity and in
the division of aid between recipients. Given diminishing returns to aid intensity, most
of the aid may be directed at the middle-income recipient initially, with the allocation
later switching towards the smaller, poorer recipient. Throughout the analysis, we assume
that the capital account is closed. This assumption is common in the literature, but some
commentators argue that poor countries do not need aid when investment can be financed by
capital inflows. In practice, capital has tended to flow to middle-income countries rather
than the poorest countries. And even when the capital account is open, there is still a
role for aid, to finance both consumption and the accumulation of assets owned
domestically. It is likely that the welfare gains from aid would be less in this case,
since initial consumption is higher; nevertheless, financing higher consumption would
remain valuable. The quantitative investigation of this would be an interesting topic for
future research.1 Since the model is stylized, it is worth clarifying the intended
contribution. The paper provides a new way of framing the decision problems facing aid
donors. The model could be extended, and made more realistic, in many directions; it is a
first step towards richer quantitative frameworks that could inform future aid policies.
The current simulations serve two more limited aims. The first is to investigate some
qualitative results about aid policies when absorption constraints matter: these results
are not special cases, but can emerge as important under reasonable parameter assumptions.
The second aim is to illustrate what might be learnt by future research using more
complicated models. For example, the current analysis is too preliminary to suggest a
replacement for the Pearson Commission benchmark, but it draws attention to some relevant
considerations. A companion paper, Carter (2014), uses related ideas to study aid
allocation rules of the type sometimes implemented by donors. The existing literature has
generally considered simpler models of North–South interactions, often in models with just
one or two periods. The majority of this work is theoretical, and studies the effects of
exogenous transfers rather than deriving their optimal time path. Some papers explore the
transfer problem, and especially the possibility of transfer paradoxes driven by terms-of-
trade effects; Eaton (1989) surveys the older literature. An alternative approach is taken
by Chamon and Kremer (2009), who construct a multi-country model in which developing
countries gradually integrate with the world economy. They discuss the potential role of
aid in accelerating this process, but aid is not included in the version of the model they
calibrate. The paper is structured as follows. The next section provides the formal
description and analysis of the donor's decision problem. Section 3 describes the
assumptions used in our simulations. Section 4 presents initial analysis of the optimal
path of aid and Section 5 extends the analysis to subsistence economies. Section 6
considers two recipients which differ in population size and income. Section 7 carries out
a sensitivity analysis and discusses potential extensions, before Section 8 concludes.

<h>THE MODEL</h>
---------

Our paper deliberately takes a narrow view of the donor's problem, seen exclusively in
terms of international resource transfers. We hope to show that even this narrow view
could inform the design of aid programs. Since the 1960s, cumulative spending on foreign
aid has exceeded three trillion dollars in nominal terms, a figure that would be even
higher in today's prices. Yet basic issues remain contested and, in some cases, rarely
studied. How generous should aid flows be, and should donors choose aid targets relative
to donor resources, or to recipient GDP? To what degree should this generosity be greater,
early in the development process? When allocating aid across multiple recipients, how
sensitive should aid flows be to recipient income levels? These are all debates that can
be informed by the approach that we develop here. We use the framework to revisit some
long-standing questions. Some of these questions concern the Pearson Commission benchmark,
which appeared in United Nations Resolution number 2626, from October 1970. The 0.70%
target was originally justified using a financing gap calculation, based on assessed
capital needs for a Harrod–Domar economy (see Clemens and Moss, 2007, for a full history).
It seems unsatisfactory to base aid policies on a model and form of analysis that are
clearly outdated. Even the basic assumption that aid should be a fixed share of donor GDP
might not be supported by a more rigorous approach. We agree with Clemens and Moss (2007)
that it seems backwards to determine aid levels based on the size of donors, rather than
conditions in recipient economies. The optimal degree of redistribution should be
dependent on the extent of between-country differences, the nature of preferences, and the
extent of absorption constraints, all of which play a role in our analysis. We formulate
the North's decisions in terms of an explicit dynamic optimization problem. The North
decides on an optimal path of transfers to the South. As in Obstfeld (1999), aid will
benefit Southern economies in two ways. Aid accelerates the rate at which the South
converges to its steady-state, and allows the South to sustain a higher level of
consumption than otherwise. Stripping the aid problem down to these two roles will clarify
their implications for aid policies and allocation decisions. In our simulations, we find
that accelerating convergence to steady-state plays only a minor role. This does not mean
the aid is wasted, however. In a model of this type, aid is effective to the extent that
it raises consumption immediately, later, or both.2 Framing the donor's problem as one of
weighted global welfare maximization has several advantages. First, the opportunity costs
of aid arise endogenously from the structure of the model. Second, our approach provides a
mapping between an explicit weight ω on Southern utility and optimal aid policies.3 We can
readily study normative questions: how generous should aid be, and what does the optimal
time profile look like? We now set out the decision problems formally. The North and South
are both characterized as Ramsey economies. We study the South's problem first, and then
the optimal control problem facing the Northern donor, where the optimizing behavior of
the South represents a constraint in the North's decision problem. To simplify the
presentation, initially we set the rates of technical progress and population growth to
zero, but the necessary extensions are straightforward. We assume that aid is ultimately
distributed to Southern households, and these are individually too small to internalize
the effects of their actions on donor policies. Hence, we can consider the donor's problem
without needing to allow strategic interactions between donors and (multiple) recipients.
That would require analysis in terms of a dynamic game, and would not be straightforward.
For the same reason, we do not model political economy forces explicitly, but these
simplifications allow an analysis that is richer in other ways.

<hs>  The decision problem for the South</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Political economy approaches often imply that some aid is wasted or diverted. Rather than
develop a specific structural model, our aid impact function translates Northern aid
donations into the actual transfers received by Southern households, allowing for wastage
or diversion.4 Our formulation nests the case where the marginal benefit of aid is
declining in aid intensity, the ratio of aid to recipient GDP. This idea has often been
investigated empirically, as in Burnside and Dollar (2000) and Clemens et al. (2012).5 One
possible story is that, as aid intensity increases, so does the proportion of aid that is
wasted or appropriated by a local elite. High aid intensity may also lead to Dutch Disease
effects. It could have adverse effects on a domestic political equilibrium, partly by
influencing rents to sovereignty, and perhaps by undermining long-term accountability and
state capacity. A proliferation of aid projects and programs could overwhelm the capacity
of the recipient government. These mechanisms have been widely discussed (see, for
example, Temple (2010)). As a consequence, it seems essential to allow for limits to
absorptive capacity. In our framework, these limits are eased by growth: as the GDP of an
aid recipient increases, the recipient can use a given amount of aid more effectively. In
the first version of the South's problem, the donor's optimal policy is not time-
consistent, due to the externality. We follow much of the literature on conditionality,
and assume that the donor has access to a commitment technology. This could take the form
of explicit commitments to aid made through domestic legislation or international
agreements that would be costly to reverse. This simplifies the analysis, and is
relatively natural given our interest in normative questions. Further, in the cases
considered below, the quantitative effects of the externality will be modest.

<hs>  The decision problem for the North</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Optimality at the initial date further requires zS0 = 0.8 In fact, the Northern planner's
problem has a solution with zSt ≡ 0 at all dates. The Southern planner internalizes the
capital externality, and the shadow value of Southern capital is the same for both
planners. The level of aid is pinned down by the first-order condition (3). The solution
is time-consistent, as the South values capital in the same way as the Northern planner.
Again optimality requires zS0 = 0, but no solution exists with zSt ≡ 0. The Northern
planner's Euler Eq. (8) would then be incompatible with the South's Euler Eq. (1) because
of the capital externality. (For example, one can see that zS > 0 in the steady-state.)
The externality leads to time inconsistency. The social returns to capital are higher than
perceived by Southern households, given the benefits of higher output for aid absorption.
To maintain the returns to capital and encourage capital accumulation, the Northern
planner is less generous to the decentralized South than it would be to a social planner
in the South. But at later dates, in the wake of past investment, the Northern planner
would like to transfer additional aid in order to increase Southern consumption. Hence,
the North's aid decision is time inconsistent. The model based on decentralized investment
decisions is arguably more realistic, and will be the focus of our simulations. When we
later examine the contrasting case of a Southern planner, the optimal generosity of aid is
similar, but with higher investment in the early stages of the transition. These effects
are quantitatively modest, suggesting that time-consistent aid paths would not look
greatly different from those under full commitment. As noted earlier, we assume that the
donor can commit to an entire path for aid flows, and leave the investigation of time-
consistent aid policies to future work, perhaps using the approach of Cohen and Michel
(1988). Contributions related to ours include Kopczuk et al. (2005), Weyl (2014) and
especially Kemp et al. (1990). The latter paper uses optimal control methods to study the
timing and generosity of aid needed to maximize weighted global welfare, just as we do. A
crucial difference with our paper is that, although they briefly acknowledge the
possibility of absorption constraints, they do not analyze them. Instead, they concentrate
on the case where the South's resource constraint is linear in aid. They show that, at
time zero, the optimal policy involves a transfer of part of the North's capital stock to
the South.9 In our work, we rule out stock transfers, a step which is a natural
counterpart to the assumption of absorption constraints, as they note. A further
difference is that Kemp et al. (1990) is purely theoretical, whereas we present
quantitative results based on simulations.

<hs>  The steady-state</hs>
  ~~~~~~~~~~~~~~~~

The first equation has a natural interpretation: the Northern donor balances the marginal
cost of aid – represented by the marginal utility of forgone Northern consumption –
against the marginal benefit of aid, namely the marginal utility of Southern consumption
weighted by ω and LS, and multiplied by the derivative of the aid impact function with
respect to aid.10 Under our assumptions, the equation has some interesting implications
when parameters are such that cN∗ > cS∗. First, under absorption constraints, it is not
optimal to equalize steady-state marginal utilities even when ω = 1. Second, it can be
shown that steady-state aid is increasing in ω, as expected. Third, another simple result
applies under isoelastic preferences: steady-state aid is decreasing in the intertemporal
elasticity of substitution. All of these results are in line with intuition. In other
respects, the externality complicates the comparative statics. We saw earlier that, with
isoelastic preferences, increasing the intertemporal elasticity of substitution reduces
the extent of global redistribution, as expected. But this is not always true in the
version of the model with an externality. In principle, there could be reasonable
functional forms and parameter values for which steady-state aid is increasing in the
intertemporal elasticity of substitution over some range. This counter-intuitive
possibility arises because the externality-related wedge term depends on the elasticity.
Since the effects of the externality are modest in our simulations, we do not pursue this
question further. The structure of the model does not rule out negative transfers. In
fact, for a sufficiently low weight ω on Southern welfare, the North may choose to
transfer income from the South to the North (‘negative aid’) at some points in time. This
never happens in our simulations for the values of ω that we consider, but would emerge
for weights close to zero. A richer analysis, at the expense of greater complexity, would
either constrain aid to be non-negative — this is what Kemp et al. (1990) call the ‘non-
cooperative’ case — or modify the aid impact function so that negative transfers are
costly for the North to implement. Note that, in our simulations, both the South and North
will start below their respective balanced growth paths. We could assume that the North is
on its balanced growth path and decides to donate a fixed share of its GDP, so that aid to
the South grows steadily over time. This would remove the need to model the North
explicitly, and Carter (2014) and Carter and Temple (2014) use this simplification. But if
we want to study aid generosity, and allow the share of aid in Northern GDP to change over
time, then the more general approach of this paper is useful. Aid generosity has
implications for Northern consumption, and modeling the North explicitly is a natural way
to capture the time-varying opportunity cost of aid.

<h>SIMULATION ASSUMPTIONS</h>
----------------------

We now describe the assumptions used in our simulations. As we noted earlier, the
simulations that we present are best seen as preliminary. This is partly because the model
is stylized, and partly because the appropriate parameter choices are uncertain. The
simulations illustrate what might be learnt from richer quantitative analyses in the
future. In the past, the broad principles of aid programs, and some of their details, have
often drawn on rather simple and unsatisfactory models, as Easterly (1999) emphasizes. The
parameter choices for preferences are relatively straightforward. We assume that σ is
equal to two, a common choice in the literature.12 We set the discount rate ρ equal to
0.03; this corresponds to the choices of Obstfeld (1999) and Gourinchas and Jeanne (2006).
Note that both σ and ρ will influence the optimal generosity of aid. For simplicity, we
assume that donors and recipients have access to a Cobb–Douglas technology with a common
exponent on capital, but different levels of TFP. We assume the exponent on capital is
0.50. This is higher than most estimates of physical capital's share of income, but some
authors argue that a broader notion of capital is needed for neoclassical growth models to
be consistent with the data: see Mankiw et al. (1992) and, especially, Barro and Sala-i-
Martin (2004). Our choice of 0.50 has been used in related contexts, such as in Kraay and
Raddatz (2007). The choice matters because it will influence the speed at which the South
converges to its steady-state, and the rate at which the marginal product of capital falls
along the transition. To explore the predictions of the model, we also need to make
assumptions about the long-run growth rates of GDP per capita and population, the size of
the South relative to the North, and their initial capital–output ratios. Data on output,
investment and population are taken from the Penn World Table version 6.3. We estimate the
capital stock for 110 countries using the perpetual inventory method over the period
1960–2007, following Bernanke and Gürkaynak (2002) and adopting their depreciation rate of
0.06. We then aggregate countries into two units, the global North (the donor) and the
global South (the recipient). The 33 countries aggregated into the Northern economy are
those with output per capita above 20,000 in 2007 international (PWT) dollars, while the
remainder are classed as the South. For our initial investigations, we sometimes exclude
China and India, with their large populations.13 This keeps the quantitative analysis
comparable with the aid decisions made in practice. As is well known, aid receipts per
capita are low for China and India, partly reflecting the ‘small country bias’ in aid
allocation; excluding these two countries helps to keep the model close to the data. This
leaves us with an aid recipient whose population size is 2.7 times that of the donor,
denoted S′ in Table 1. The final two columns of Table 1, S1 and S2, show the South sub-
divided into low and middle income recipients, for use in Section 6. The cut-off of 20,000
international dollars roughly corresponds to the upper quartile of the GDP per capita
distribution. We then calculate total output, capital stock and population for the two
regions, for the most recent year in the PWT 6.3 data (2007), making no distinction
between population and labor force. This procedure yields a capital–output ratio for each
region. Since we assume Cobb–Douglas production functions for both North and South, the
capital–output ratios imply the initial levels of capital per effective worker. We can
then infer the relative TFP and GDP per capita of the South. We assume that rates of
technical progress and population growth are the same for donor and recipient, helping to
ensure a balanced growth path. The first assumption is common in the empirical growth
literature. We adopt a rate of technical progress of 2% a year, as in Mankiw et al.
(1992). This is also approximately the average growth rate in our Northern group of
countries for the most recent decade in the data. The assumption that population grows at
the same rate in donor and recipient can be justified as a long-run outcome, given that
population growth rates are falling in the developing world. We assume that the long-run
population growth rate is 1.5% a year. This is approximately the average rate over the
last decade in the Southern group of countries, but somewhat higher than in the North over
the same period. Under these assumptions, the North begins the simulation with capital per
effective worker about 10% below its steady-state value (see the ‘N’ column of Table 1). A
convenient way of interpreting this function is to ask when aid intensity at/YSt is
sufficiently high that the marginal benefit of aid is zero for the South. This happens
when at/YSt = υ/2. The appropriate severity of this absorption constraint is a matter of
debate. In our baseline, we set υ so that an extra dollar of aid has zero impact when the
aid/GDP ratio is 25%.14 A final choice relates to ω, the relative weight of Southern
utility in the objective function of the North. The use of such a weight seems essential
to any normative study of transfers between the North and South. We are not seeking to
estimate the weight that Northern citizens currently adopt, nor to defend a particular
choice of ω on prior grounds. Instead, our framework provides a mapping between
assumptions on ω and optimal aid generosity. A possible parallel would be with Kopczuk et
al. (2005), who build on the earlier work of Mirrlees (1971): these papers allow a mapping
between alternative degrees of inequality aversion and tax rate schedules. In our
simulations, we choose a baseline weight ω = 0.1 to represent a donor that is genuinely
altruistic, but imperfectly so. We will investigate later how optimal aid changes when ω
takes higher values. As we will see, even the choice of ω = 0.1 — so that Northern
citizens have ten times the welfare weight of Southern citizens — can lead to shares of
aid in Northern GDP substantially higher than in the data.

<h>OPTIMAL AID POLICIES</h>
--------------------

In this section, we study the optimal time path for aid using simulations. To do this, we
use the relaxation algorithm of Trimborn et al. (2008) to solve the system of differential
equations implied by the optimal control solution. In our baseline case, aid generosity
should be highest at the beginning, so that the South accelerates towards its steady-
state. But this front-loading result is sensitive to absorption constraints. There are
scenarios in which the North should increase the generosity of its aid (relative to its
GDP) as the South grows, since the South can then absorb a given level of aid more
effectively. The first panel of Fig. 1 shows the optimal path of aid in our baseline case.
Aid relative to Northern GDP is initially 7.1%, falling to 4% after 17 years and to 2.4%
in steady-state. Aid flows on this scale are clearly too high to be realistic, and were
not seen even under the Marshall Plan.15 Importantly, however, long-run generosity is
highly sensitive to the assumed curvature of the utility function. If we reduce σ by just
10%, to σ = 1.8, the North will continue to be generous early on, but much less so at
longer horizons. Hence, diminishing returns to consumption can provide a powerful
motivation for international transfers, but at longer horizons, parameter assumptions
matter a great deal. Moreover, it is likely that the North places even less weight on the
utility of the South than we are currently assuming. There are other possible reasons for
the divergence between the model and the flows observed in practice. We do not model the
marginal cost of public funds: aid is financed by lump-sum taxation rather than
distortionary taxes. Nor do we incorporate any political economy constraints on the donor,
such as taxpayer resistance to large international transfers. Hence, natural extensions to
our model would yield smaller ratios of aid to Northern GDP for given values of ω and σ.
Aid intensity in the South is initially 16.8%, falling to 3.3% in the long run. Fig. 1
also shows the effect of aid on the rate at which Southern output and consumption converge
towards Northern levels, and the effect of aid on the Southern saving rate (expressed as
the deviation from a zero-aid counterfactual). The front-loading of aid enables the South
to raise consumption by 14.4% immediately. The effect of aid on growth is familiar from
Obstfeld (1999): there is an initial, but modest, acceleration which is eventually
followed by slower growth relative to the autarky counterfactual. Growth is ultimately
slower because aid brings capital accumulation forward, so that capital is accumulated
quickly early on and more slowly later. Even though aid intensity is high in this baseline
calibration, the effect on output growth is small. In annual terms, the initial growth
rate is 0.57 percentage points higher, with the difference eliminated after 14 years;
roughly 25 years later, the growth rate is 0.08 percentage points lower than it would have
been without aid. It may seem surprising that the growth and welfare effects of aid are
not larger. It is clear that, with isoelastic utility, exogenous transfers of this
magnitude have only limited effects on optimal investment. The explanation is that, when
the benefits of investment are high, it will be undertaken even in the absence of
transfers, because forgoing consumption is not costly under these preferences. Hence
Obstfeld (1999) finds modest growth effects, and he notes (p. 136) that the result is
‘likely to be a robust feature of any plausible model in which aid is funneled through the
private sector’.16 More broadly, our results on welfare effects are also consistent with
the work of Gourinchas and Jeanne (2006) on capital mobility. They showed that the welfare
benefits of capital inflows in a calibrated Ramsey model are unexpectedly modest. This is
partly because convergence will be rapid even in the absence of foreign capital, and
partly because accumulating capital more rapidly brings forward a reduction in its
marginal product. This intuition is helpful in understanding why the effects of aid on
productivity are also relatively modest in our setting. But in the case of aid, we can
take this logic further: if relaxing the South's resource constraint is not all that
valuable to the South, it is likely that tightening the North's resource constraint is not
all that costly to the North. This is why we find large transfers to be optimal, even
though the productivity benefits of a given transfer are limited. Scenarios in which aid
increases over time are shown in Figs. 2 and 3. For some combinations of ω (the weight on
the South's utility) and υ (the aid absorption parameter) it may be optimal for the North
to back-load aid: as the South develops, it becomes better able to use aid effectively,
and the North should increase the generosity of aid relative to its GDP. What happens if
the North gives a fixed share of its GDP, as in the Pearson Commission 0.70% benchmark?
When the fixed share is chosen optimally, the welfare losses for the South relative to the
fully-flexible optimal aid policy are modest. Perhaps counter-intuitively, if the North
has to donate a fixed share of GDP, the costs of this restriction are sometimes borne by
the North in equilibrium: the North becomes more generous in the long run than it
otherwise would, and the South sometimes does better than it otherwise would.17 We also
find that, if aid is fixed as a share of Northern GDP, departures from the optimal choice
of this share are not particularly costly: the donor's objective function is relatively
flat as a function of the aid share. Fig. 4 compares outcomes when the North can vary aid
as a share of its GDP, and when the share is fixed. By construction, the donor must always
do at least as well when free to choose a flexible path for aid, but the effect of fixing
the share on the donor's objective is surprisingly modest. In our baseline case, the
associated utility loss is equivalent to an ongoing reduction in consumption of 0.2% for
the North and South. Looking at the two economies individually, the restriction to a fixed
share leaves Northern households worse off (− 0.8 %) and Southern households better off (+
0.6 %). But this is not always the case. For some cases with higher ω, the restriction to
a fixed share leaves the North better off and the South worse off. The role of ω hints
that these results arise from the interplay of the benefits of aid at short horizons, the
benefits at long horizons, and whether fixing the aid share is wasteful due to absorption
constraints. Finally, we limit aid to the Pearson Commission benchmark, 0.70 % of Northern
GDP. Compared to our optimal flexible path, the much lower generosity means that the HEV
welfare gain in the South falls from 11% to 2%.

<h>OPTIMAL AID FOR SUBSISTENCE ECONOMIES</h>
-------------------------------------

We now consider preferences with a subsistence level of consumption. It is well known that
the single-sector Ramsey model with isoelastic preferences makes some unrealistic
predictions: fast convergence to the steady-state, and a sharp decline in investment rates
and in the marginal product of capital as capital is accumulated. Nor can it readily
accommodate periods of international divergence in GDP per capita, or explain why
investment rates are sometimes low in poorer countries. Ben-David (1998) and Steger (2009)
argue that Stone–Geary (SG) preferences overcome these problems. Low investment can co-
exist with high returns to investment, because the opportunity cost of investment is high
when households are close to subsistence. We examine the implications for the generosity
and timing of aid, including whether donors will want to front-load aid. As expected,
under SG preferences, aid generosity should be high early in the development process. We
present some results in Fig. 5, which could be compared with the earlier CRRA results in
Fig. 1. The optimal level of aid is initially higher under SG preferences, at 9.6% of
Northern GDP. It declines to the same asymptotic level of 2.4% (recall that the CRRA and
SG growth paths are asymptotically equivalent) but converges to this level more slowly in
the SG case. Under SG preferences, Southern output converges more slowly towards the
Northern level. This is a natural result: when the Southern economy is close to
subsistence, the opportunity cost of investment is high. But the optimal time path for aid
helps to close the gap between North and South to a greater extent under SG preferences
than under CRRA preferences. This is another natural result, since relaxing the
intertemporal resource constraint is more valuable in the SG case. The effect of SG
preferences on the generosity of aid means that aid has a greater impact on consumption in
the SG case. The peak change in consumption, relative to autarky, is similar (17% under
SG, 14% under CRRA) but the duration of the effect on consumption differs greatly. Under
SG preferences, Southern consumption is 11% higher than the zero-aid counterfactual 50
years after the commencement of aid. Under CRRA preferences, the equivalent figure is just
6%. This difference reflects the greater generosity of aid in the SG case: aid is 5.5% of
Northern GDP at t = 50 under SG preferences, but just 2.5% under CRRA. Although the
absolute change in the initial annual growth rate, relative to the zero-aid
counterfactual, is similar to the CRRA case at 0.59 percentage points, autarky output
growth is slower under SG preferences, at 3.5% per year.18 So the impact of aid on growth
with SG preferences is more substantial, multiplying the initial growth rate by 1.17,
compared with a multiple of 1.08 under CRRA preferences. To compare the SG and CRRA cases
in more detail, Fig. 6 shows outcomes based on the same fixed quantity of aid.19 The
higher aid intensity in the SG case reflects the fact that Southern output grows more
slowly under these preferences. The effects of aid on net investment, consumption and
growth are markedly greater in the SG case. Since our assumptions on preferences vary
across the two cases, more direct welfare comparisons are not meaningful.

<h>OPTIMAL AID WITH TWO RECIPIENTS</h>
-------------------------------

In this section, we study the donor's problem when there are two aid recipients.
Additional recipients can be integrated into the Northern planner's optimal control
problem in the obvious way. With multiple recipients, allocation decisions are connected
because aid to one country reduces consumption in the North, increasing the opportunity
cost of aid to other countries. We construct a low-income recipient, S1, using the
countries in the lowest quarter of the GDP per capita distribution. The other recipient,
S2, is an aggregate of ‘middle income’ countries, defined as those between the lower and
upper quartile of the GDP per capita distribution. Table 1 lists some of the relevant
numbers. We now include China and India, unlike in our baseline case. As a result, the
middle-income country is ‘large’: the population of S2 is 6.1 times greater than the
population of S1. Output per capita in S2 is about 19% that of the North, whereas the poor
recipient, S1, has output per capita only 5% that of the North. Hence, in this first
experiment, output per capita in S2 is about four times greater than in S1. The long-run
ratio of output per capita between the two is smaller, however, at 2.5. This is because
the initial capital stock in S1 is further beneath its long-run level than S2. The ratio
k0/k∗ is 0.13 for S1 and 0.35 for S2. Hence, without aid, S1 initially grows faster than
S2: annualized growth is 13% for t = 0 in S1, 6% in S2. This calibration can address an
important policy issue: does low consumption help to motivate aid even for middle-income
countries? Fig. 7 illustrates the optimal aid allocation under CRRA preferences. The
contrast between the two recipients is striking. A substantial amount of aid is allocated
to the middle-income recipient, and its response is familiar from our baseline case. But
despite the poor recipient S1 starting further beneath its balanced growth path, and with
greater scope for aid-induced growth, the effect on investment (which mirrors the effect
on output convergence) is negligible. Instead of a front-loaded aid path that induces
accelerated investment, the donor keeps aid intensity high throughout and increases
generosity in absolute terms over time. This reflects the aid absorption constraint: the
donor cannot be too generous to S1 initially, because the optimal quantity of aid already
takes this economy close to the point where the marginal benefit of aid is zero. The
recipient S1 uses aid to fund a higher level of consumption, with little change in
investment behavior, because this recipient correctly anticipates that aid will increase
over time. As for the middle-income recipient S2, where the population is larger and the
absorption constraint is less binding, the donor is generous early on but then scales aid
back over time as the recipient grows. This is reflected in the shares of the two
recipients in total aid: the middle-income recipient receives the bulk of the aid at
shorter horizons, and the low-income recipient S1 at longer horizons. To explore further,
we change the population of S2 so that it matches that of S1. Fig. 8 shows what happens:
there is a sharp reduction in the quantity of aid given to S2, but qualitatively the paths
are unchanged. The level of aid given to S1 is virtually unchanged, despite the large
reduction in aid given to S2 with an associated reduction in the opportunity cost of aid
to the North. This result arises because S1 is already being given as much aid as it can
effectively absorb.20

<h>SENSITIVITY ANALYSIS</h>
--------------------

In this section, we carry out some sensitivity analyses, and then discuss possible
extensions. First, recall the externality that arises in our setup: capital accumulation
by Southern households increases the ability of the South to absorb aid. What happens if
we take our baseline calibration and assume Southern decisions are made by a social
planner? The optimal policy for the Northern planner now leaves Northern households
slightly worse off (equilibrium aid is slightly more generous) and the South slightly
better off. The effects on the North are modest and the optimal path for aid barely
differs, compared to the decentralized version. The peak difference in aid between the two
cases, as a percentage of Northern GDP, is only 0.7 percentage points. But the change in
Southern consumption is noticeable: the Southern planner anticipates the favorable effect
of investment on future aid absorption, and chooses higher investment rates in the first
few years of the transitional dynamics. Overall, however, the quantitative importance of
the externality is modest. We discuss these results in more detail in an online appendix.
Next, we briefly consider the effects of varying two parameters: σ, the curvature of the
utility function, and α, the output–capital elasticity. In modifying these parameters, we
still require the Northern and Southern capital–output ratios to match those in the data.
Relative to our previous experiments, there is a direct effect of changing each parameter,
and an indirect effect which arises from matching the observed capital–output ratios under
new parameter assumptions. The alternative route, of only focusing on the direct effect,
would lead to an inconsistency between the capital–output ratios in the simulations and
those in the data. As noted earlier, the curvature of the utility function has a major
effect on optimal generosity, especially at longer horizons. When the marginal utility of
consumption diminishes less rapidly with consumption, the motivation for global
redistribution is weakened. In our simulations, with slightly less curvature (σ = 1.8
rather than σ = 2.0) aid generosity is reduced and the effect on consumption is smaller.
Given technical progress, the level of the balanced growth path is raised by a reduction
in σ, and the effect of aid on growth is initially stronger than in our baseline. This
effect is modest, however. Increasing the output–capital elasticity has similarly
complicated effects. It makes aid more effective, since capital accumulation becomes more
important; it also raises the balanced growth path. We do not present the results in
detail, but note that as α increases, the effect of aid on investment is lower but the
effect on growth larger. Intuitively, because investment now has greater benefits, the
South is able to consume more early on. We now briefly discuss some possible extensions.
Perhaps the most important modification to the analysis would be to introduce political
economy considerations within the South. This would introduce a major complication, namely
strategic interactions between the donor and recipients. One possibility would be to allow
aid to finance public investment, as in Chatterjee et al. (2003) and other work summarized
in Turnovsky (2009); see also Lowe et al. (2013). Expenditure on public investment
projects could be wasteful to some degree, with the extent of waste increasing in
expenditure as in Berg et al. (2013). Politics in the North could also play a role: in
principle, the North's objective function could reflect the North seeking political
influence, as in the work of Antràs and Padró i Miquel (2011). Another extension could
allow aid recipients to borrow internationally, with a risk premium that is increasing in
external indebtedness. van der Ploeg and Venables (2013) examine the optimal response of
recipient governments to windfall revenues in such an environment, but treat the time path
of revenues as exogenous, which seems better suited for natural resource windfalls than
aid flows. Perhaps their decision problem could be integrated within that of an altruistic
North, using the nested structure we adopt here. A related extension would model
recipients as two-sector economies that produce traded and non-traded goods, in which case
absorption constraints could arise endogenously through Dutch Disease effects. Staying
closer to our current framework, other possibilities include country-specific population
and technical progress dynamics, costs of distortionary taxation in the donor, adjustment
costs in the North for aid disbursements, finite-duration aid commitments by the donor,
CES production technologies, and the introduction of capital varieties; see Hoxha et al.
(2013) on the latter. A more ambitious extension would introduce output volatility in the
South, so that aid would have an additional insurance role. This would bring the analysis
closer to Arellano et al. (2009), at the expense of greater computational complexity.

<h>CONCLUSIONS</h>
-----------

This paper has introduced a framework for analyzing optimal aid policies using the
neoclassical growth model. In contrast to most previous research, the findings are based
on a clearly-defined optimization problem for the Northern donor. It takes into account
the opportunity cost of aid, optimizing behavior by Southern households, and constraints
on the effective absorption of aid. This framing of the problem is a first step in the
direction of a richer quantitative analysis, and the simulations indicate what might be
learnt from future exercises of this type. Since any tractable model must be stylized,
there will always be a need for subjective judgments on the part of donors; but formal
models can make visible some considerations and possibilities that would otherwise be
obscure. We find that optimal transfers are influenced by the weight a donor places on
recipient welfare, the curvature of the utility function, the recipient's capacity to
absorb aid, the relative level of the recipient's balanced growth path, and the
recipient's initial distance from that growth path. In our simulations, the scope for aid
to raise growth rates plays some part in aid decisions, but the effect on the level of
consumption often dominates. The optimal generosity of aid, relative to Northern GDP,
should vary over time to reflect conditions in aid recipients. In our baseline case, aid
generosity declines over time. But in some scenarios, where donors run up against
absorption constraints, there is a time interval over which generosity should be
increasing. As for optimal aid intensity — that is, aid relative to Southern GDP — this
should generally decline over time. But in cases where the aid absorption constraint is
close to binding, the optimal policy may dictate that high aid intensity is maintained for
a long time. In the case of multiple recipients, the optimal policy may involve large
changes over time in the absolute quantity of aid and the division of aid between
recipients. As expected, the case for donor generosity is strengthened when consumption is
close to subsistence. The effects of aid on Southern consumption, investment and growth
can be dramatic in this case. In general, our numerical results indicate optimal aid
levels that exceed those in the data, at least at short horizons. An interesting task for
future research is to pin down the features of reality that could explain this disparity.
That citizens of donor economies may place little weight upon the welfare of aid
recipients is only one possible explanation; others could include the potential roles of
political economy forces and corruption in undermining the effectiveness of aid. Given the
obvious importance of these considerations, our approach is a partial view. Nevertheless,
it provides some insights and results that could help to inform the design of aid
policies, and is simple enough to be extended in many directions.


<h>REFERENCES</h>
----------

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  [11] Santanu Chatterjee, Georgios Sakoulis, Stephen J. Turnovsky. Unilateral capital transfers, public investment, and economic growth. doi:10.1016/S0014-2921(02)00235-0
  [12] Michael A. Clemens, Todd J. Moss. The ghost of 0.7 per cent: origins and relevance of the international aid target. doi:10.1108/14468950710830527
  [13] Michael A. Clemens, Steven Radelet, Rikhil R. Bhavnani, Samuel Bazzi. Counting Chickens when they Hatch: Timing and the Effects of Aid on Growth. doi:10.1111/j.1468-0297.2011.02482.x
  [14] Daniel Cohen, Philippe Michel. How should control theory be used to calculate a time-consistent government policy?. doi:10.2307/2297581
  [15] William Easterly. The ghost of financing gap: Testing the growth model used in the international financial institutions. doi:10.1016/S0304-3878(99)00047-4
  [16] Jonathan Eaton. Chapter 25 Foreign public capital flows. doi:10.1016/S1573-4471(89)02012-7
  [17] Paul J. Gertler, Sebastian W. Martinez, Marta Rubio-Codina. Investing cash transfers to raise long-term living standards. doi:10.1257/app.4.1.164
  [18] Pierre Olivier Gourinchas, Olivier Jeanne. The elusive gains from international financial integration. doi:10.1111/j.1467-937X.2006.00393.x
  [21] Indrit Hoxha, Sebnem Kalemli-Ozcan, Dietrich Vollrath. How big are the gains from international financial integration?. doi:10.1016/j.jdeveco.2013.02.003
  [22] Ravi Kanbur, Andy Sumner. Poor countries or poor people? Development assistance and the new geography of global poverty. doi:10.1002/jid.2861
  [24] Wojciech Kopczuk, Joel Slemrod, Shlomo Yitzhaki. The limitations of decentralized world redistribution: An optimal taxation approach. doi:10.1016/j.euroecorev.2003.08.004
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<ART>Dynamic supply adjustment and banking under uncertainty in an emission trading scheme: The market stability reserve
================================================================================

Authors: Sascha Kollenberg, Luca Taschini
DOI: 10.1016/j.euroecorev.2019.05.013
Year: 2019  |  Pages: 213-226
ASJC codes: 2002, 2003
Keywords: EU ETS Reform, Policy Responsiveness, Resilience, Risk-Aversion, Supply Management Mechanism

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We study the impact of a supply management mechanism (SMM) similar to the Market Stability Reserve proposed in 2015 which preserve the overall emissions cap and we comment on the recent cap-changing amendments. We provide an analytical description of the conditions under which an SMM alters the emissions abatement paths, affecting the expected length of the banking period and its variability. While abatement strategies of risk neutral firms solely depend on the former, for risk-averse firms changes in the latter would lead to higher risk premia, accelerated depletion of the bank and, consequently, further reduction of abatement and allowance prices. Cancellation of part of the reserve could partially outweigh the effect on risk premia sustaining allowance prices.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Despite an emerging use of supply control mechanisms, in most existing cap-and-trade
programmes the environmental reduction target (the cap) is fixed and the supply of
allowances is inflexible and determined within a rigid allocation programme. In theory, as
long as the regulator makes allowances available before they are needed, the programme
will deliver a cost-effective solution Hasegawa and Salant (2015). However, observations
from recent cap-and-trade schemes – in particular the European Union Emissions Trading
System (EU ETS) – have raised concerns over excessive allowance price variability and
price collapse. These maladies seem to stem from a problem of ‘over-supply’, wherein
unexpectedly low levels of allowance demand have led to the accumulation of a significant
surplus of allowances. An article in The Economist (2013) lamented a surplus of allowances
equivalent to an average year’s emissions. This surplus is often attributed to two
effects. On the one hand, the economic recession and renewables-promoting policies have
led to a significant drop in allowance demand; on the other, the system has been unable to
respond to changes in economic circumstances and policies, see Grosjean et al. (2014) and
Ellerman et al. (2015). The resultant drop in allowance prices has policy makers and other
stakeholders concerned that the current imbalance in supply and demand, if left unchecked,
could reduce incentives for low-carbon investment and ultimately impair the ability of the
EU ETS to meet its targets.1 There are already provisions within a cap-and-trade framework
that, in theory, should compensate for unforeseen changes in allowance demand. For
example, most ETSs have banking provisions that should provide firms with a tool to
respond to demand shocks. Several studies have explored the effect of banking and
borrowing provisions as cost ‘smoothing’ mechanisms which decrease allowance price
variability; Hasegawa and Salant (2014) provide a comprehensive and critical review of the
literature on bankable emissions allowances that has developed over the last two decades.
Other studies demonstrate how hybrid systems, combinations of quantity- and price-based
instruments, lower expected control costs ultimately mitigating allowance price
variability (Fell and Morgenstern, 2010; Grüll and Taschini, 2011; Fell et al., 2012b;
2012a). However, these provisions alone may not be sufficient when the market is faced
with severe demand shocks. This leads to the question of how to amend an existing ETS to
deal with an unexpected under- or over-supply of allowances. Namely, how should the
allowance allocation programme (the supply, which can be controlled by regulators) be
changed to better cope with unexpected changes in allowance demand. In the case of the EU
ETS, the European Commission (EC) has proposed a structural reform of the ETS, including
the implementation of the Market Stability Reserve (MSR) that has started to operate in
2019 (EC, 2014a; 2014b; EP, 2015). The MSR amends the allowance allocation programme. In
particular, it adjusts the number of allowances auctioned based on the size of the
aggregate bank, i.e. the sum of firms’ individually held banks of allowances. Hereafter,
we refer to quantities concerning the entirety of regulated firms as ‘aggregate’ whereas
the respective quantities for each firm are referred to as ‘individual’. In a given year,
if the aggregate bank of allowances exceeds 833 million, a pre-defined percentage of the
size of the aggregate bank will be withheld from auctions and will be placed in a
dedicated reserve. There are two intake rates: 24% from 2019 to 2023 and 12% from 2024.
These allowances are returned to the market in batches of 100 million as soon as the
aggregate bank drops below the threshold of 400 million. In its original 2015 design, the
MSR changes the allowance allocation programme but leaves the total number of allocated
allowances (the cap) unchanged within the regulatory period. As such, the reserve is
temporary in nature and the initially proposed version of the MSR preserves the original
cap. The alternatives of temporarily versus permanently placing allowances in the reserve
have been heartily debated in the past years. In late 2017, after numerous stakeholder
consultations and more than two years of negotiations, the European Commission decided
that, starting in 2023 the volume of allowances that can be held in the reserve will be
capped at the previous year’s auction volume. The resulting difference in the reserve will
be cancelled, providing a mechanism for allowances to be retired and thus reduce the long-
run supply of allowances. In an earlier paper (Kollenberg and Taschini, 2016), we examined
a similar dynamic allocation programme where the cap could be varied in response to
exogenous shocks, as is the case for the 2017 version of the MSR. Accordingly, the
applicability of this earlier framework to the original 2015 MSR is limited. With the
additional objective to comment on the recent proposed MSR amendments (allowances
cancellation), we focus our analysis on a generalised, cap-preserving supply management
mechanism (SMM for short) similar to the original 2015 MSR legislation. The proposed SMM
allows us to abstract from the operational details of the EC MSR2 and to provide a
conceptual framework that enable us to transparently illustrate (1) how firms’ abatement
strategies vary in response to changes of the allowance allocation programme and (2) how
an SMM affects the risk-premium associated to holding allowances or any equivalent
investment in abatement. As such, we draw from and contribute to the literature on inter-
temporal permit trading under uncertainty and to the emerging literature on the assessment
of mechanisms that vary allowance allocation according to market conditions, such as
indexed regulations (among others, Newell and Pizer, 2008; Kollenberg and Taschini, 2016;
Lintunen and Kuusela, 2018), output-based allocation (Meunier et al., 2017), and price-
based mechanisms (Aldy et al., 2017). In particular, the implications of the changes in
risk-premia speak directly to the policy debate playing out among experts on no-cap
adjustments versus cap adjustments. Our analysis ultimately suggests that a permanent
cancellation of part of the reserve could keep in check the premium that risk-averse firms
demand for abatement investments. As a by-product, the relevance of our findings extends
to the policy debate in California, South Korea and the member States of the Regional
Greenhouse Gas Initiative, where similar supply management mechanisms were adopted. The
results of previous theoretical and empirical analyses of intertemporal trading of
emission allowances reveal that, under the usual assumption that marginal abatement costs
are increasing in emissions reduction, firms start accumulating allowances and then draw
them down, see Rubin (1996), Schennach (2000), Ellerman and Montero (2007), and Ellerman
et al. (2015). Banking of allowances is thus a manifestation of the inter-temporal trading
problem. The rationale for banking is quite intuitive: if tomorrow’s discounted expected
cost is higher than today’s cost, it is worth banking allowances, whether obtained by
abating more emissions today or by purchase, and either using them to cover some of
tomorrow’s emissions or selling them later on. The expected duration of the banking
period, i.e. the period of time during which firms prefer to hold allowances, depends on
the amount of abatement implied by the cap and, as long as the original abatement path is
feasible (see Perino and Willner, 2016), it is independent of the allowance allocation
programme. In the analysis that follows, we explore the impact of an SMM on firms’
abatement strategies using a model of the inter-temporal pollution control and allowance
trading. We consider the inter-temporal optimisation problem of each entity in a continuum
of small regulated firms. At each point in time, each firm has to decide by how much she
wants to offset her individual emissions, considering current and future costs of reducing
emissions, as well as her existing individual bank of allowances and future allowance
demand and allocations. The chief decision state variable is the firm’s expected required
individual abatement, the difference between counterfactual emissions (individual
cumulative emissions in the absence of emissions restrictions) and the number of
allowances individually allocated. Every firm adjusts her abatement and trading strategies
at each time t based upon this state variable, taking into account her current bank of
allowances and any change in the required abatement. Under uncertainty, changes in firm’s
expectation about the required individual abatement affect how much individual abatement
and banking will occur in the future – and for how long. We thus frame our analysis of the
impact of a cap-preserving mechanism that amends the allowance allocation programme,
similar to the 2015 version of the MSR, in terms of two main state variables: firms’
expectations about the required abatement and the length of the banking period. Previous
studies have demonstrated that firms’ strategy adjustments and the overall efficacy of the
2015 MSR are highly dependent on the constraints on temporal provisions (i.e. limitations
on borrowing) and on the design of the mechanism implemented to adjust the allowance
allocation, see Salant (2016), Perino and Willner (2016), Fell (2016). In the absence of
borrowing constraints, abatement decisions are independent of the temporal distribution of
allowances. If firms can always borrow from future allocations, any change to the
allocation programme that maintains the overall emissions cap is irrelevant. Firms will
simply borrow the required allowances needed to remain on their original cost-minimised
emissions path and the adjustments of the allowance allocation programme will have no
influence. Under borrowing constraints, a change in the allocation programme can affect
abatement and allowance price paths only when the amount of allowances presently available
to firms to cover emissions is insufficient. This is the availability condition in Salant
(2016) or the feasibility condition in Perino and Willner (2016). Our analytical results
are consistent with these results: an SMM can only change abatement and allowance price
paths if and only if the onset of the SMM changes the expected required abatement, i.e.
the expected future net demand of allowances. Specifically, abatement strategies are
unaltered when neither the expectation about the length of the banking period (τ) nor the
post-SMM expected required abatement change. Conversely, when the adjustments in the
allowance allocation programme determined by an SMM affect the expected required
abatement, the expected length of the banking period τ and its distribution vary.3 When
considering the impact of previously unexpected changes (e.g. demand shocks), we note that
changes to the timing of allowance allocation can affect the instantaneous likelihood of
the event of an instantaneous depletion of the bank. We term this instantaneous breakdown.
That is to say, changes to the distribution of τ by an SMM can change the probability that
firms are not able to compensate for a demand shock with their current individual bank of
allowances. This is related to the discussion of price variability in Perino and Willner’s
analysis. They show that the short-term scarcity produced by the (binding) MSR can drive
prices up and increase price volatility when allowances are removed from the market. Our
findings support the conclusion that a cap-preserving supply control mechanism increases
price variability overall. Crucially, changes in price volatility due to an SMM are
immaterial for risk neutral firms. Their abatement strategies solely depend on the
expected required abatement. However, for risk-averse firms, differences in price
volatility matter and should be reflected in the risk premium demanded by those firms for
holding allowances or for investing in abatement. Thus, we expand our analysis to risk-
averse firms and show that changes in the probabilistic distribution of τ brought on by an
SMM that lead to higher price variability (compared to no-SMM) generate higher risk
premia. The higher the risk premium, the more quickly firms will deplete their bank, which
leads to lower levels of abatement and lower prices. However, abatement and allowance
prices are affected to a lower extent during different periods of the bank. Thus, compared
to the no-SMM case, the consequence of higher price variability are more compelling when
regulated firms are not perfectly risk-neutral. This could have significant implications
for the overall impact of an SMM like the MSR proposed in 2015. While one of the goals
some stakeholders attributed to the original MSR was to increase prices during periods of
over-supply, the building up of the allowance reserve by a cap-preserving mechanism would
have the opposite effect. When the behaviour of risk-averse firms is taken into account,
the impact of an SMM is more striking: the rise in price volatility would lead to higher
risk premia, accelerated depletion of the bank and, consequently, abatement and prices are
reduced even further. Cancellation of part of the reserve could partially outweigh the
effect on risk premia and sustain allowance prices. The remainder of the paper is
organised as follows. In Sections 2.0 and 2.1 we describe the model assumptions and define
the key decision making variables for each of the agents on the allowance market. In
Section 2.2 we present the market equilibrium in terms of aggregate quantities and provide
an analytical description of the conditions under which an SMM alters the emissions
abatement paths. In Section 2.3 we relax the assumption of risk neutrality and explore the
effect of an SMM on a time-dependent risk premium. Section 3 concludes.

<h>THE MODEL: FIRMS’ POLLUTION CONTROL PROBLEM</h>
-------------------------------------------

Regulated firms are assumed to be atomistic in a perfectly competitive market for emission
allowances. Firms face an inter-temporal optimisation problem where, at each point in
time, they have to decide how much they want to offset their emissions (either by abating
or by trading allowances), considering the current and future costs of reducing emissions.
Each firm accounts for her current individual bank of allowances and the number of
allowances she expects to be allotted in the future. In this context, the required
abatement, the difference between the cumulated individual amount of emissions without
abatement requirements (counterfactual individual emissions) and their future allocation,
is the key quantity each firm has to assess at each point in time. Under uncertainty,
changes in a firm’s expectation about the required abatement affect how much abatement and
banking will occur in the future – and for how long. Crucially, the impact of these
changes is relevant only during the banking period. Once the bank is depleted, the inter-
temporal problem breaks down: each firm uses every allowance available to cover
contemporaneous individual emissions and instantaneously abates her residual individual
emissions (Schennach, 2000).4 Thus, we focus our analysis on the banking period [0, τ) and
investigate under which conditions an SMM can alter the length of the banking period τ and
its probabilistic distribution.

<hs>  Required abatement under uncertainty</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

To capture the impact of uncertainty on banking in a cap-and-trade programme under the
SMM, we identify two key state variables of the system: the time-t expectations of (i) the
instant τ when the aggregate bank is completely depleted and (ii) the corresponding
required aggregate abatement, that is counterfactual emissions over [0, τ) minus the total
number of allowances allocated in the same period (including the initial aggregate bank of
allowances). When new information becomes available, firms update their expectations and
adjust their strategies. That is, abatement and trading strategies are adapted at each
time t, taking into account the current aggregate bank of allowances and the change in the
required aggregate abatement.

<hs>  Equilibrium solution for risk-neutral firms</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The following analysis extends the efforts of these authors by studying how a cap-
preserving supply control mechanism affects price volatility and – under risk aversion –
the risk premium associated to the instant when firms prefer to deploy their bank. The
rationale is the following: under risk aversion the impact of an SMM on price volatility
is reflected in the risk premium and, consequently, in firms’ discount rate. The latter
signals whether returns from allowance-related investments should promise higher or lower
returns with consequent effects on allowance banking.

<hs>  Changes in expectations: a dynamic view and risk-aversion</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

During the building up of the allowance reserve, the change in allowance allocation
increases the likelihood of an instantaneous breakdown. This is reflected in an adjustment
of the risk-premium qt. More precisely, Eq. (6) reveals that a change in gt generates a
change in σt which equally transfers to a change in qt. Consequently, risk-averse firms
adjust their abatement behaviour, as quantified in Eq. (5). As previously discussed, the
impact of qt on abatement is larger in the short term, when the expected end to the
banking period lies in the distant future and the SMM is removing allowances from the
market. Thus, in the short run the potential losses associated to abatement investments
due to an instantaneous breakdown are high. As time goes by, the expected time τ of
complete depletion of the aggregate bank approaches and allowances from the reserve are
released. As we can see from Eq. (5), the reduction in qt is determined by the combined
effect. Abatement and allowance prices increase, but to a lower extent than both were
decreased earlier during the building up of the reserve. In conclusion, we find that under
risk aversion, the changes brought on by the SMM to the distribution of the instant when
firms prefer to use their entire aggregate bank, lead to higher price variability –
compared to the risk-neutral case – and, consequently, higher risk premia. However, we
note that the impact of a change in the likelihood of an instantaneous breakdown affects
prices and abatement more in the short run than it does in the long run. These findings
corroborate concerns about rising price volatility, as raised by Perino and Willner (2016)
and Fell (2016).

<h>CONCLUSIONS</h>
-----------

The supply of allowances in the European Union Emissions Trading System (EU ETS) has been
inflexible and determined within a rigid allocation programme. As such, the system lacked
provisions to address severe imbalances in demand and supply of allowances resulting from
economic shocks. In 2015 the European Commission proposed a structural reform of the EU
ETS, including the implementation of a Market Stability Reserve (MSR), operative since
2019. The MSR will adjust the allowance allocation programme based on the aggregate bank
of allowances: In times of a large bank, allowances are transferred to a dedicated reserve
to be released in times of scarcity. In its original 2015 design, the MSR preserves the
total number of allowances issued over the regulatory phase. After two years of
negotiations and an extensive impact assessment, the European Commission decided that
allowances held in the reserve above the previous year’s auction volume will no longer be
valid. The findings of our work support the decision for regular cancellation of excess
allowances. We develop a stochastic equilibrium model of inter-temporal trading of
emission allowances to investigate under which conditions a supply management mechanism
(SMM) similar to that proposed for the EU ETS can alter allowance price and emissions
abatement paths. Similar mechanisms were adopted in California and South Korea. We show
that the timing of allocation is largely irrelevant as long as changes in expected net
demand of allowances are such that the resulting bank remains essentially unaltered.
Conversely, when the transitory scarcity brought on by the SMM changes the net allowance
demand, the mechanism affects the expected abatement and the price paths. In this context,
we consider unexpected changes in firms’ expectations that triggers an instantaneous
depletion of the bank of allowances (what we termed unexpected breakdown). Risk neutral
firms are indifferent to changes in the variability of this event. However, when firms
account for the risk in the change of the variability of their future required abatement –
i.e. counterfactual emissions minus total number of allowances allocated over the same
period – and equivalently, risk in the variability of the value of their abatement
investments, adjustments in the allowance allocation programme matter. We then expand our
analysis to study how risk-averse firms’ strategies are affected by an SMM at different
points in time of the banking period. We show that changes in the distribution of the time
of the unexpected breakdown brought on by the SMM lead to higher price variability and,
consequently, higher risk premia. The higher the risk premium associated with holding
allowances, the more quickly firms will deplete their bank, which is associated with lower
levels of abatement and, importantly, lower allowance prices. This has clear policy
implications for the current debate on cap adjustments vs. no-cap adjustments: the
influence of a generalized, cap-preserving supply management mechanism like the 2015
version of the MSR could be counter-productive, especially when the behaviour of risk-
averse firms is considered. Importantly, while increased price variability in the short
run may prevail even under the amended MSR, (the anticipation of) a permanent cancellation
of part of the reserve will, at the very least, lead to lower risk of low-carbon
investments (such as purchase of allowances) and, accordingly, higher prices in the short
run with lower but less risky long-run returns. The late 2018 increase in allowances
prices to almost three times its value since the amendment of the MSR may well be
attributed to a market perception of such decreased risk.


<h>REFERENCES</h>
----------

  [4] A. Denny Ellerman, Juan Pablo Montero. The efficiency and robustness of allowance banking in the U.S. Acid Rain Program
  [7] Harrison Fell. Comparing policies to confront permit over-allocation. doi:10.1016/j.jeem.2016.01.001
  [8] Harrison Fell, Ian A. MacKenzie, William A. Pizer. Prices versus quantities versus bankable quantities. doi:10.1016/j.reseneeco.2012.05.004
  [9] Harrison Fell, Richard D. Morgenstern. Alternative Approaches to Cost Containment in a Cap-and-Trade System. doi:10.1007/s10640-010-9377-2
  [10] Harrison Fell, Dallas Burtraw, Richard D. Morgenstern, Karen L. Palmer. Soft and hard price collars in a cap-and-trade system: A comparative analysis. doi:10.1016/j.jeem.2011.11.004
  [11] G. Grosjean, W. Acworth, C. Flachsland, R. Marschinski. After monetary policy, climate policy: is delegation the key to EU ETS reform?. doi:10.1080/14693062.2014.965657
  [12] Georg Grüll, Luca Taschini. Cap-and-trade properties under different hybrid scheme designs. doi:10.1016/j.jeem.2010.09.001
  [13] Makoto Hasegawa, Stephen Salant. Cap-and-trade programs under delayed compliance: Consequences of interim injections of permits. doi:10.1016/j.jpubeco.2014.07.006
  [14] Makoto Hasegawa, Stephen Salant. The dynamics of pollution permits. doi:10.1146/annurev-resource-100913-012507
  [15] Sascha Kollenberg, Luca Taschini. Emissions trading systems with cap adjustments. doi:10.1016/j.jeem.2016.09.003
  [16] Jussi Lintunen, Olli Pekka Kuusela. Business cycles and emission trading with banking. doi:10.1016/j.euroecorev.2017.10.015
  [18] Richard G. Newell, William A. Pizer. Indexed regulation. doi:10.1016/j.jeem.2008.07.001
  [19] Grischa Perino, Maximilian Willner. Procrastinating reform: The impact of the market stability reserve on the EU ETS. doi:10.1016/j.jeem.2016.09.006
  [20] Jonathan D. Rubin. A model of intertemporal emission trading, banking, and borrowing. doi:10.1006/jeem.1996.0044
  [21] Stephen W. Salant. What ails the European Union׳s emissions trading system?. doi:10.1016/j.jeem.2016.06.001
  [23] Susanne M. Schennach. The economics of pollution permit banking in the context of Title IV of the 1990 Clean Air Act Amendments. doi:10.1006/jeem.1999.1122
<ART>Early gender gaps among university graduates
============================================

Authors: Marco Francesconi, Matthias Parey
DOI: 10.1016/j.euroecorev.2018.02.004
Year: 2018  |  Pages: 63-82
ASJC codes: 2002, 2003
Keywords: Field of study, Gender wage gap, Germany, University graduates

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We use data from six cohorts of university graduates in Germany to assess the extent of gender gaps in college and labor market performance twelve to eighteen months after graduation. Men and women enter college in roughly equal numbers, but more women than men complete their degrees. Women enter college with slightly better high school grades, but women leave university with slightly lower marks. Immediately following university completion, male and female full-timers work a very similar number of hours per week, but men earn more than women across the pay distribution, with an unadjusted gender gap in full-time monthly earnings of about 20 log points on average. Including a large set of controls reduces the gap to 5–10 log points. The single most important proximate factor that explains the gap is field of study at university.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Since the influential survey by Altonji and Blank (1999), the economic literature has
offered a variety of new explanations about gender gaps. Bertrand (2010) provides an
insightful review of recent contributions, drawing on advances in the psychology and
experimental literatures. Her review emphasizes the importance of gender differences in
risk preferences, attitudes toward competition and negotiation, and the strength of other-
regarding preferences as well as the importance of social norms that may induce
differential sorting of men and women across occupations.1 In another recent survey
looking at a large sample of high-income countries, Olivetti and Petrongolo (2016) stress
the role played by changes in the industry structure with the shift from manufacturing to
services, which might have increased female employment and reduced (but not eliminated)
the gender wage gap. We make use of a unique data source which allows us to analyze a
representative survey of six cohorts of university graduates between 1989 and 2009 from
all fields of study and across the range of Higher Education institutions in Germany, soon
after they complete their college education. The survey also follows the same individuals
five to six years into their careers. In this paper we focus only on the first snapshot
after graduation. The reason is that career opportunities within the firm (which may
involve firm-specific investment, or ability to negotiate with employers, or internal
promotions) as well as other crucial family-related decisions (such as starting a family
and committing resource allocations within the household) are likely to be less relevant
than later on in life.4 Our results indicate that 12–18 months after graduation, the raw
(unadjusted) gender gap in full-time monthly earnings is about 20 log points on average,
even though male and female full-timers work relatively similar hours. Including a large
set of controls reduces (but does not eliminate) the gap to 5–10 log points, with the lion
share in the reduction being accounted for by field of study. In light of this, assessing
the extent of gender gaps and deepening our understanding of their nature within a human
capital paradigm seem important steps, before looking for alternative explanations
related, for example, to psychological cues, attitudes, social norms, and biomarkers. Our
analysis provides new evidence for Germany on a variety of facets of gender gaps. We
consider two broad sets of outcomes. The first refers to the educational performance of
men and women while they are at university and explores gender differentials in enrolment
rates, marks at university entry (i.e., secondary school grades), graduation rates and
graduation marks. The second set refers to early labor market performance and focuses on
gender differences in the probability of having a full-time job and in pay within 12–18
months after graduation. Existing analyses of gender gaps in Germany focus on wage
differentials among all workers and not just university graduates, while gender
differences in university attainments have not yet been fully explored.5 Using social
security data, Fitzenberger and Wunderlich (2002) document large and persistent gaps
between 1975 and 1995: they estimate that West German full-time female employees earned
about 35% less than their male counterparts at the beginning of that period, and the gap
went only slightly down to about 25% at the end. These figures refer to all workers and
may not apply to the most educated workforce, where censoring in the administrative data
occurs frequently. In a more recent assessment with data from the 1996 Labor Force Survey,
Machin and Puhani (2003) find that the (raw) gender wage difference among university
graduates in Germany is about 28 log points, and about 40% of the explained gap can be
accounted for by field of study. By looking at graduates across all ages, however, these
differences will in part reflect choices and constraints that emerge well after
graduation. Using data from the European Community Household Panel over the 1995–2001
period, Arulampalam et al. (2007) observe an unconditional average wage gap of 20%.
Conditional on covariates, they find an increasing profile of the gap along the wage
distribution ranging from 6 to 17% among public sector workers and from 14% to 20% among
workers in the private sector. Analyzing administrative data, Huffman et al. (2017)
confirm the large gaps found in the earlier studies and show that roughly half of the 29%
raw gap in 2008 is accounted for by observables, including age, schooling, establishment
size, collective bargaining status, and industry dummies.6 A number of institutional
features specific to Germany may potentially not be gender neutral and may thus influence
our outcomes of interest.7 One of such features is that Germany tracks student into
different schools based on ability as early as the end of elementary school (ages 10–12).
There is evidence that early tracking has no lasting effect on later wages, employment,
and occupational choice (Dustmann et al., 2017). However tracking may give differential
penalties or advantages by gender (e.g., Pekkarinen, 2008 for Finland). For example, if
girls mature earlier than boys during secondary school years, they could perform better in
school irrespective of the track chosen, and this in turn could affect their relative
performance later on, at university and in the labor market. Alternatively, more
competitive boys might disproportionately attend the top school tracks, and this might in
turn affect performance at university or in better-paid jobs. Our analysis will assess the
extent of differential performance in secondary school among university graduates and
consider whether this in turn has an impact on outcomes. Another feature is that, since
the late 1970s, Germany has also developed (and provided working mothers with) generous
maternity leave coverage, whereby mothers are currently eligible for three years of
partially paid leave. Analyzing the impact of five major expansions in maternity leave
coverage occurred between 1979 and 1993, Schönberg and Ludsteck (2014) find that the
impact of such expansions on overall maternal employment, employer continuity, and labor
market income 3–6 years after childbirth is small. The small magnitude of the impact could
be the result of pre-labor market selections, either into school track or field of study
and occupation. In our work, we focus on the role of decisions and human capital
accumulation inside the university and education system, such as field of study. Our work
is related to a number of existing studies which focus on highly skilled individuals,
primarily in the United States. Bertrand et al. (2010) study the careers of men and women
who gained a master's degree in business administration (MBA) from a top US business
school between 1990 and 2006. They find that, 10–16 years after MBA completion, the male
(unadjusted) earnings advantage is nearly 60 log points. Differences in business school
courses and grades, differences in career interruptions and differences in weekly hours
worked are identified as the three most important explanations for the large and rising
gender gap. Interestingly, important differences are observed also at the outset of men
and women's careers. One year after MBA completion, men earn approximately 15% more than
women. Although the gap goes down to about 6% after controlling for a large set of
characteristics (e.g., pre-MBA characteristics, MBA performance, labor market experience,
and weekly hours), it remains statistically significant. Looking at pharmacists, Goldin
and Katz (2016) find that conditioning on hours of work reduces the gender earnings gap
from about 28% to 4%–7%. Among those without children, female pharmacists earn only 1%
less than comparable male pharmacists, and this difference is not statistically
significant. It is unlikely, however, that this pattern is observed across the range of
other professional occupations, and it is part of our objectives to explore this for
Germany.8 Two recent studies look at the experience of countries other than the United
States. Building on the previous work by Albrecht et al. (2003), the first study is by
Albrecht et al. (2017). They analyze Swedish matched employer-employee data on men and
women born in the 1960s who completed their university education in business and economics
and are followed for 20 years after graduation.9 At the start of their careers, at age of
25–26 years, men and women have virtually the same monthly full-time equivalent wages, but
by age 45 there is a sizeable gender wage gap of about 25 log points. Albrecht et al.
(2017) argue that, over and above the differences in firm characteristics and firm-to-firm
mobility by gender, the main driver of the gap appears to be the greater wage gains
experienced by men as opposed to women. The second study by Bütikofer et al. (2017) looks
at Norway. Using detailed register data, they focus on the effect of parenthood on the
careers of men and women with MBA, law, medical, and STEM degrees.10 They show that, among
top earners, the share of women holding a degree in all subjects, except medics, has
increased substantially since the mid 1980s. Interestingly, when focusing on men and women
at the start of their careers, the average earnings prior to childbirth are identical in
levels for men and women. As illustrated by Bertrand et al. (2010) for American MBAs, also
in Norway differences in career interruptions that are associated with childbirth lead to
substantial pay gaps by gender, which do not decline even ten years after childbirth.11
Comparing to our findings, our results indicate that the differentials faced by young
German male and female college graduates are somewhere in between those faced by their
American and Scandinavian counterparts. Section 2 describes our main data source. Section
3 presents the main results related to gender gaps at entry into, and exit from,
university. Section 4 discusses the estimates found in relation to gender gaps in the
labor market. Finally, Section 5 summarizes our main findings, contrasts them with the
existing literature, and puts forward a number of areas for future work.

<h>DATA</h>
----

We analyze the trajectories of college graduates using survey data collected by the German
Centre for Higher Education Research and Science Studies (DZHW). These data come from
nationally representative longitudinal surveys of individuals who complete their
university education across all fields of studies and the full range of Higher Education
institutions in Germany.12 The DZHW sampled university graduates from the graduation
cohorts 1988–89, 1992–93, 1996–97, 2000–01, 2004–05, and 2008–09.13 This gives us a large
sample of high-skilled individuals spanning a 20-year period. For each graduation cohort,
individuals are first interviewed about 12-18 months after graduation. The same
individuals also participate in a second, follow-up survey about five years after
graduation (see Appendix Fig. A.1). In our analysis we focus only on the first survey: as
we have explained above, this allows us to abstract from crucial decisions other than
those related to early careers (e.g., family formation and fertility choices) and from
later career opportunities (which involve internal promotions and negotiation with
employers). Each survey contains detailed information on graduates’ personal
characteristics, family background, study history, and labor market experience. For each
graduate, we observe the university attended and the field of study completed.14 We
complement this information with administrative data published by the German Federal
Statistical Office. Although the DZHW data have been gathered systematically across
cohorts, there are some differences in the information available across the cohorts. For
instance, information on marks from the exams (known as Abitur) taken at the end of the
academically oriented secondary school track (Gymnasium) are not available for the 1989
cohort. We therefore present two sets of estimates, either excluding the 1989 cohort or
dropping the secondary school mark variable from the analysis. Table 1 reports the summary
statistics of key variables from the DZHW data. High school marks are scored on an
approximately continuous scale from 1 to 4, where 1 is the top score and 4 is the lowest
passing mark. On average, across all cohorts, female graduates enter university with a
slightly better mark, showing a gap of 0.065 points which is statistically significantly
different from zero at conventional levels and represents about 10% of a standard
deviation. University final score is measured on the same scale, with 1 and 4 meaning top
and lowest passing marks, respectively. At the end of their university career, women also
graduate with slightly better marks than men across all cohorts (again statistically
significant). However, as we document in our subsequent analysis, these aggregate average
statistics conceal heterogeneity across cohorts. About 87% of females and 88% of males
have ever been in any kind of employment since graduation and up to the survey. Between 12
to 18 months since graduation, about 71% of women are in paid full-time employment
(relative to part-time employment), as opposed to 81% of men. The large 10 percentage
point difference is statistically significant. Among full-timers, the mean number of hours
worked per week is around 40, with no significant difference between men and women.
Average full-time monthly log earnings (excluding additional bonuses or variable pay) are
7.587 (corresponding to just below 2000 Euros, measured in 2001 prices) for all workers
across all graduation cohorts, with men earning 28.3 log points (or nearly one-third) more
than women.15 This difference is statistically significant. In terms of median earnings
(not reported in the table), the members of the 2009 DZHW cohort have median monthly
earnings of 1747 Euros for women and 2329 Euros for men (including full-time and part-time
workers). Among full-time workers, median earnings in the 2009 cohort are 2183 and 2620
Euros for women and men, respectively (in 2001 prices). At the time of interview, men are
older, suggesting that women tend to obtain their degrees earlier than men.16 It is worth
noticing that male and female graduates are also different along a number of other
observable, predetermined characteristics. For instance, almost one-third of men have
completed an apprenticeship before starting their degree, as opposed to only one-quarter
of women. Moreover, compared to their male counterparts, female graduates have parents
(both mothers and fathers) with substantially higher education, greater labor market
involvement, and in higher-level occupations. For example, female graduates’ mothers have
on average almost 0.9 more years of education, compared to their male counterparts (which
partly reflects time trends in share of females and parental education).

<h>GENDER GAPS IN UNIVERSITY EDUCATION</h>
-----------------------------------

To see if there are compositional differences in university education we first analyze
enrolment rates by sex. We then look at potential gender differences in “quality” at entry
into college, which we proxy with the Abitur grades obtained before starting a university
program. Next, we consider the possibility of differential graduation rates by sex, since
those who complete their program of study should be more likely to be in graduate
employment than those who do not complete. Finally, we look at gender gaps in graduation
marks, which are taken as a indicator of quality of the university qualification attained
and could be a relevant proxy (for ability or productivity) which is easily observed by
employers.

<hs>  Gaps in the quantity at entry: enrolment numbers</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

There might be a “quantity” imbalance at entry, that is, differential female–male
enrollment into university courses. To explore this possibility, we investigate enrollment
counts by gender, using aggregate administrative data on university enrollment.17 Fig. 1
shows the trends from 1947 to 2015. From the beginning of the period to 1989, the data
refer to the former West Germany only, while from 1990 onwards the data has coverage of
the whole of Germany, including the former German Democratic Republic. From the post-WWII
period to the early 1990s, substantially more men than women entered a college program,
with a female-to-male student ratio of 0.4–0.6. By 1995 and up to the most recent data
point, however, the numbers have become very similar.18 The share of females enrolled has
therefore steadily increased since 1995, from a ratio of 0.91 per male student, and
reaching parity in 2015, when we observe a ratio of 1.002.

<hs>  Gaps in the quality at entry: high school grades</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

New male entrants into post-secondary education institutions may have greater high school
marks than their female counterparts. We assess this possibility by looking at gender
differences in Abitur grades, conditional on having obtained a degree. Grades range
between 1 (top) and 4 (lowest passing grade) on an approximately continuous scale. The
pooled mean of 2.23 and standard deviation of 0.63 have remained fairly constant across
cohorts and the cohort-specific distributions are also relatively similar. Panel A in
Table 2 reports  the female coefficient from a series of regressions. In the first row, we
only control for cohort dummies; while in the second we also include apprenticeship
status, and family background variables (all predetermined characteristics at the time of
university enrollment) as well as age, and in the third we further control for subject and
university fixed effects. Notice that a negative sign means that women have a better mark
than men, because values are on a reverse scale. Across all graduation cohorts, women
enter university with slightly better high school marks (row (i)). The size of the
uncorrected gap is 0.069 (or about 0.11 of a standard deviation in high school score).
Correcting for predetermined characteristics reduces the gap to 0.015 (or 0.02 of a
standard deviation, row (ii)). In fact, men in the earlier cohorts (1993 and 1997) have
better marks, corresponding to a period when also more of them enrolled (see Fig. 1): in
such cases, the size of the gender gap is about 0.05 (0.07–0.08 of a standard deviation).
But from 2005 onwards, women have substantially higher entry marks, of the order of
0.12–0.13 of a standard deviation. This ‘overtaking’ is a phenomenon also highlighted by
Fortin et al. (2015) for the United States, although in our case we consider only
individuals who actually enroll at university and complete their university studies, and
not all secondary school students. Controlling for field of study and institution fixed
effects leads to a gap of about 0.07 of a standard deviation across all subjects (row
(iii)). Panel B of Table 2 shows there is heterogeneity across specific degree areas,
although the broad pattern emerges within each field. Among those who enroll in medical
sciences and economics/business, women tend to have better secondary school marks. This is
not the case among those who enroll in STEM (which are typically male dominated) and
humanities subjects (which are typically female dominated). In summary, our starting point
is to assess whether there are gender differences when men and women start their
university careers, over the period that pertains the DZHW data. There is a greater
fraction of men enrolling at university up to the mid 1990s, when men also had a small
advantage in terms of quality at entry. In the most recent data, however, women and men
enter college in equal numbers and female graduates begin their university careers with
slightly better high school marks.

<hs>  Gaps in the quantity at exit: graduation numbers</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We now move to the end of the university process and focus on two graduation outcomes. We
first consider whether there are differences in the quantity of female graduates as
opposed to male graduates. To describe the time trends in the numbers of male and female
graduates, we use administrative data on the number of graduates by field of study. Fig. 2
reports the raw numbers, while Fig. 3 shows the corresponding female/male ratios. From the
early 1990s to the mid 2010s, the total number of graduates has gone up from 181,000 in
1993–339,000 in 2015 (see panel (a) in Fig. 2), implying an increase of about 87% over the
period (an average increase of nearly 4% every year). The share of all graduates
represented by women has also increased from about 40% in 1993 to approximately 52% in
2015, or equivalently from a female/male ratio of 0.66 to a ratio of 1.09 (see Fig. 3).
Some fields of study, such as fine art, art history, and humanities (including foreign
languages), have been traditionally female dominated, with 60–70% of graduates in the mid
1990s being women. Over time, they have become even more female dominated, with 65%–75% of
graduates being women in 2015 (see panels (c) and (f) in Fig. 2). Conversely, other
fields—such as science, technology, engineering, and mathematics (STEM)—were male
dominated in the 1990s and continue to be so in the 2010s, although the share of all
graduates represented by women has increased from about 15% to almost 25% in engineering
and computing and from around 35% to 40% in all hard sciences and mathematics (see panels
(d) and (g) in Fig. 2). Clear increases for women in graduation rates can be observed in
health sciences (including medicine and pharmacy), social sciences (including law,
business studies, economics and psychology), and agricultural studies (including nutrition
science). In the first two areas of study, in particular, the growth in the number of
female graduates has been quite remarkable (see panels (e) and (h) respectively in Fig. 2,
as well as Fig. 3): up by about 12 points in the case of social sciences (from 44% to 56%
of all graduates) and up by nearly one quarter in the case of health sciences (from 45% to
almost 70%). Notice that both the time trend over our sample period and the actual
fraction of female graduates in all health science programs in Germany are very similar to
those shown by Goldin and Katz (2016) for pharmacists in the United States.

<hs>  Gaps in the quality at exit: graduation grades</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

A second outcome at exit is degree quality, which is measured by the final graduation
mark. To assess whether there are gender gaps in grade performance, we use data from
across the six DZHW cohorts and perform three different exercises.

     <hss>Means</hss>

            In the first exercise we estimate five different specifications of a final
            grade equation, keeping in mind that marks range from 1.0 (best) to 4.0 (worst
            passing mark), and thus a positive sign indicates lower marks for female
            graduates. Using data pooled across five cohorts (excluding 1989) and with a
            regression that controls for survey wave dummies, we find a small (but
            statistically significant) gender gap at 0.022 points (s.e.=0.006) that favors
            men (see column (a) of Table 3). This difference corresponds to just 0.032 of
            the sample grade standard deviation. The addition of demographic and
            socioeconomic controls to the regression increases the gender gap to 0.04
            points (column (b)), suggesting that the lower marks obtained by women are
            unlikely to reflect differences in socio-demographic and family background
            variables. Adding high school marks, field of study fixed effects, and
            university fixed effects (columns (c)–(e)) leads to gradually higher gender
            gaps reaching 0.063 points (column (e)), which corresponds to 0.09 of a
            standard deviation. These estimates demonstrate that conditioning on
            covariates to control for differences in individual characteristics and family
            background, high school results, subject of study, and university attended
            does not eliminate the small grade gender gap that favors men over women. In
            fact, if anything, such differences magnify the grade gender gap, although
            this remains arguably modest. These patterns are in line with the descriptives
            presented in Table 1 above. When such estimates are disaggregated by
            graduation cohort (see Table 4, panel A), we find a strong time gradient,
            whereby the gap is about twice as large at the beginning of the 1990s as it is
            in 2009. The estimates in panel B, where we do not control for high school
            marks (and therefore the 1989 cohort also contributes to the analysis) show an
            even stronger gradient. Although the gap at the start of the sample period is
            almost 0.1 points in favor of men, in 2009 this is 70% smaller. Comparing the
            results in panels A and B suggests that accounting for high school marks
            accentuates the gender difference in terms of graduation marks from 2001
            onwards. This is in line with the significant differences in terms of high
            school marks seen in Table 2(iii) for these cohorts, and the strong link
            between high school grades and graduation marks.

     <hss>High marks</hss>

            By looking at linear mean regressions we cannot detect nonlinearities. With
            the second exercise, therefore, we examine whether there are gender
            differences at the top of the final grade distribution. This allows us to see
            if there are different effects of gender among high achievers. Using the same
            specifications employed for the mean graduation marks regressions before, we
            estimate linear probability models in which the dependent variable takes value
            one if an individual obtains a graduation marks of 1.5 or better (i.e., a mark
            between 1 and 1.5), and zero otherwise. The results from this analysis are
            reported in panels C and D of Table 4, where, besides the full set of
            controls, we investigate the role of secondary school marks as additional
            control. Irrespective of this inclusion, we find that, across all graduation
            cohorts, women are 3.5–4 percentage points less likely than men to graduate
            with top marks, a nontrivial effect that corresponds to about 14%–16% of the
            sample average probability of obtaining a mark at 1.5 or better. An important
            question, therefore, is to understand what happens during the college career
            of male and female students, given that women start university with an
            indicator of higher quality (i.e., better secondary school grades). In part,
            this might be due to a higher dropout rate among men (since equal numbers of
            men and women enroll and more women graduate), something however we cannot
            test directly with our data. Dropout rates are substantial: for students
            starting 2006/07, Heublein et al. (2012) estimate dropout rates for Bachelor
            students in Germany at 35% at universities, and 19% at universities of applied
            sciences. Comparing across genders, males are found to have a 6–10 percentage
            points higher dropout rate (at universities, 38% for males versus 32% for
            females; at universities of applied sciences, 23% for males versus 13% for
            females). If academically weaker men abandon their university studies (and do
            so more than women), each cohort of graduates could be composed of
            academically stronger men. This in turn may be reflected in their performance
            in the labor market, which we will analyze in the next section. Of course,
            there could be other explanations, for instance, universities might have
            academic curricula that fit men’s abilities better than women’s, or build
            men’s skills more efficiently than women’s. These questions are an interesting
            issue for future work.

     <hss>Heterogeneity by field of study</hss>

            In the last exercise, we look at differences in graduation marks in the four
            subject categories we already analyzed above (economics/business, STEM,
            humanities, and medical sciences). These have different gender compositions
            (e.g., humanities are female dominated and STEM subjects are male dominated)
            and have gone through major changes in terms of gender representation in the
            last two decades, as shown in Figs. 2 and 3. Table 5 reports the gender gap
            estimates by cohort, using the same specification as that shown in panel A of
            Table 4, i.e., including secondary school marks in all regressions. There is
            large effect heterogeneity across degree subjects. Male graduates in STEM
            subjects and humanities have better marks at graduation than women. The
            difference over all cohorts is 0.13–0.18 of a standard deviation in graduation
            marks and is statistically significant at conventional levels. In the
            humanities, the gap has become smaller (and statistically insignificant) for
            the most recent graduation cohort, while in STEM subjects the gap has remained
            fairly constant over time. In economics/business, where the fraction of male
            and female graduates is more similar, the gender differential is substantially
            smaller, and we cannot detect any significant gap. As documented earlier,
            medical studies have witnessed a rapid and considerable increase in female
            graduates. In this field, the gap (favoring men) has grown among graduates in
            the most recent cohorts, when fewer men obtain medical related degrees. This
            might indicate an increasing positive selection of men into medical subjects.
            We close this section with a summary of its main results. We emphasize six
            findings. First, since the mid 1990s, roughly equal numbers of men and women
            enroll in Higher Education programs in Germany. Second, conditional on having
            completed college, women enter university with better secondary school marks.
            Third, at the end of their university career, more women than men obtain a
            degree. Fourth, there is some persistent educational specialization by gender,
            with substantially more men in STEM subjects and more women in arts and
            humanities, although this segregation has lessened in recent years. Fifth,
            female graduates do not outperform male graduates in terms of final exit
            marks. The difference reveals a better performance among male graduates. This
            is clearer when we look at the top of the final university grade distribution,
            whereby men are 3.5 percentage point more likely to obtain top grades than
            women over the whole sample period. Sixth, gender gaps in graduation marks
            differ by field of study. When we pool graduation cohorts, we detect larger
            differentials among graduates in the humanities and STEM subjects. The
            reversal of relative performance at the end as opposed to the start of the
            university career is interesting and, to our knowledge, new.

<h>GENDER GAPS IN THE LABOR MARKET</h>
-------------------------------

To assess the extent of gender differentials in the labor market we begin with an analysis
of the earnings gap among full-time workers observed 12–18 months after graduation. We
will start by looking at differences at the mean, but then also analyze effects across the
earnings distribution. We then consider the gender difference in the probability of being
in full-time employment and the number of hours worked. Finally, we perform a
decomposition analysis of the earnings gap so that we can better gauge the role played by
different sets of predictors, especially those that are not normally observed in
nationally representative datasets, such as university attended and fields of study.

     <hss>At the mean</hss>

            Table 6 reports estimates of the gender gap obtained from different sample
            selections and with or without the inclusion of different sets of correlates.
            To avoid issues related to choices or constraints which we do not model here,
            we focus on full-time workers only. The gender gap in full-time earnings over
            the whole period is 28.7 log points, including only graduation cohort and
            state dummies (row (i)). This is remarkably close to the figures reported in
            Machin and Puhani (2003), although those refer to all graduates, and not just
            recent graduates. The temporal pattern of the gap is only slightly negative,
            going down from 34 log points in 1989 to only 24 in 2009. This gap may in part
            reflect a differential propensity by gender to enter into different types of
            paid professional training (e.g., lawyers, medical doctors, and teachers) or
            to start a salaried doctoral program of study. Although paid, both training
            programs and Ph.D. studies are likely to be paid below market wages. Excluding
            individuals in training or Ph.D. programs leads to the estimates shown in the
            second row (row (ii)). About 30 per cent of the sample are dropped, and the
            gender gap becomes one-third smaller, but without a clear time trend.
            Selecting the sample further (i.e., requiring the availability of secondary
            school marks data, and thus dropping the 1989 cohort) leads to virtually
            identical gender gap estimates (row (iii)). The inclusion of a large set of
            controls (i.e., personal characteristics, family background variables,
            graduation university score, university fixed effects, and field of study
            fixed effects) reduces, but does not eliminate, the gender pay gap. When all
            individuals are included (row (iv)), this goes down to 7.8 log points for all
            cohorts pooled together, a reduction of more than 70% in comparison to the
            estimates shown in the first row. We also see a more pronounced reduction over
            time, with the gap almost halving from 10.1 log points in 1989 to 5.6 log
            points in 2009. The inclusion of controls in the sample in which men and women
            in professional training or doctoral programs are excluded (row (v)) leads
            also to a smaller gender gap than in the case without controls in row (ii).
            The reduction is about 55%–60%, with a resulting gender gap of 8.4 log points
            (across all cohorts). Once we account for covariates therefore we obtain
            similar estimates of the gap irrespective of whether we exclude or include the
            subpopulation of individuals in professional training or Ph.D. programs.
            Controlling for secondary school (Abitur) marks does not affect the estimated
            gap regardless of the selection on training (rows (vi) and (vii)), nor does
            the inclusion of weekly hours worked (row (viii)), although this last addition
            can only be assessed for the 2009 cohort (because detailed information on
            hours of work among full-time workers was collected only for the 2009 cohort).
            Previous research has emphasized the importance of the relationship between
            pay and hours, with nonlinearities indicating a higher career cost of family
            (Goldin and Katz, 2016). If there is linearity, a worker who works, say, 80
            hours a week will be paid twice as much as another worker who works 40 hours.
            Female full-timers may earn less than their male counterparts, but this might
            be entirely driven by the fewer hours they work; and women might deliberately
            choose to work fewer hours because they wish to have greater flexibility and
            balance job and family responsibilities. The results in Table 6 suggest that
            hours differences do not play a major role in driving gender earnings gaps in
            our context, since including hours worked in the analysis does not eliminate
            the pay differential between men and women.19 The estimates in Table 6 are
            remarkably close to those reported by Bertrand et al. (2010) for the Chicago
            MBAs at 1–3 years since MBA receipt. There are two striking features in this
            similarity. The first is that our estimates refer to a different country, with
            a different school system, and different labor market institutions, employment
            protection laws, and maternity leave regulations. The second is that they
            emerge across all university graduates in Germany, not just those in the
            corporate and financial sectors in which MBA holders are typically employed
            and where it is known that women are not getting ahead fast enough (e.g.,
            Bertrand and Hallock, 2001; Philippon and Reshef, 2012; Wolfers, 2006). A
            formal decomposition of the earnings gap using gender differences in means of
            the explanatory variables and the coefficients from the specification in line
            (v) of Table 6 shows that the single most important contribution to the mean
            level of the gender earnings gap across all graduation cohorts is given by
            field of study (see Table 7). This proximate factor alone can account for 9.4
            log points of the explained difference between male and female earnings (or
            83% of the 11.3 log point explained average gap). The same occurs when we
            examine each graduation cohort separately. Similar results also emerge when we
            analyze the larger sample that does not exclude graduates in professional
            training and Ph.D. programs (see Appendix Table A.1). Leuze and Strauß find
            that descriptively those subjects with high share of females tend to be
            associated with lower labor market returns. These findings are consistent with
            the evidence put forward by Machin and Puhani (2003) for Germany and the UK,
            even though their study focuses on all graduates and not just those who are
            observed one year to 18 months since graduation. They are also consistent with
            recent evidence that shows that different fields of study have substantially
            different labor market payoffs, even after accounting for individuals
            characteristics and awarding institution (e.g., Kirkeboen et al., 2016).

     <hss>At Different Quantiles</hss>

            One well established result for Sweden is that, although male and female wages
            are close to equal at the bottom of the wage distribution, they become
            extremely unequal at the top of the distribution (Albrecht et al., 2003),
            where presumably there is a greater concentration of college graduates.
            Similar evidence of greater gender differences at the top is also found among
            recent cohorts of full-time American workers (Blau and Kahn, 2017) and English
            graduates (see Britton et al., 2016). For Germany, Gallego-Granados and Geyer
            (2015) find that the gender wage gap decreases for higher quantiles, while
            Antonczyk et al. (2010) find a U-shaped gender wage gap.20 In what follows, we
            explore the gender earnings gap at different percentiles of the distribution
            for university graduates. Fig. 4 shows the results. Regarding the raw gender
            difference, we observe a larger gender pay gap among lower paid graduates than
            among their better paid counterparts. To investigate what share of the raw gap
            can be explained by the covariates, we use the decomposition method described
            in Chernozhukov et al. (2013). The results are reported in Appendix Table A.2.
            It is striking that once our rich set of covariates is controlled for, the
            gender wage gap is very similar across the quantiles, at around 7% (see Table
            A.2). As a result, the variables we use in our models can explain
            substantially more at the bottom of the distribution than at the top. We find
            that our covariates explain 65%–75% of the gap in the bottom three deciles,
            but only 30%–40% in the top two deciles. Interestingly, further results (not
            shown for space constraints) show that this pattern is essentially driven by
            the role of major choice, this is in line with the results in Table 7.

<hs>  Full-time employment and hours</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Previous research has emphasized that a major reason gender differences in earnings are
observed is due to differences in job experience and hours, and a large part of such
differences comes from job interruptions, with most job interruptions being due to
children (Angelov et al., 2016; Bertrand et al., 2010; Bütikofer et al., 2017; Goldin and
Katz, 2016; Goldin and Mitchell, 2017; Juhn and McCue, 2017; Sasser, 2005; Wood et al.,
1993). By looking at gaps occurring 1–1.5 years out since graduation, we are likely to
mitigate most of these channels which possibly emerge only after a longer time span. Here
we explore the role played by the differential selection into full-time employment and by
differences in weekly hours of work. Table 8 shows the results of this analysis. In the
first two columns we report the estimates from linear probability models in which the
dependent variable equals 1 if individuals are in full-time employment, and 0 part-time.
Even soon after graduation, female graduates show a significantly lower propensity to be
employed in a full-time job. When we consider all cohorts together, the (raw) employment
gap is 9 percentage points (column (a), where we only control for cohort dummies). This
gap has varied between 7 and 13 percentage points between 1989 and 2005, while only among
graduates from the 2009 cohort do we observe a substantial reduction in the gap to less
than 6 percentage points. When we include the whole set of (individual, family background,
pre-university and university) controls, the gender employment differential becomes
considerably smaller, less than 2.5 percentage points among graduates across all cohorts,
but still statistically significant (column (b)). For the most recent cohort, however, we
find a reversal in the gap, with female graduates experiencing a greater likelihood of
being employed full time by 1.1 percentage points than their male counterparts, although
this gap is not statistically significantly different from zero. Standard decomposition
analysis shows that field of study plays again a major role in explaining the gap by
gender (not reported for the sake of brevity). In columns (c) and (d), we take advantage
of additional detailed information on forms of employment other than full- and part-time
jobs, such as employment in temporary jobs and freelance work. This information is only
available from the 2001 cohort onwards. The results show that, in the most recent cohort,
women are 3–4 percentage points more likely to be ever employed than their male
counterparts. The last two columns of Table 8 (columns (e) and (f)) display the estimates
on the gender differences in hours worked. These refer to the 2009 cohort only because, as
mentioned before, information on hours of work for full-time employees was collected in
the 2009 round but not in the earlier waves. Every week women work about 0.2 fewer hours
than men. When all controls are included, the gap grows to about 0.39 hours a week. This
difference of around 25  min of work per week is statistically significant and accounts
for about 12% of a standard deviation in hours worked. The difference cannot account for
more than 15% of the 6 log point difference between male and female pay found for the 2009
cohort (see Table 6, row (viii)). Thus, hours of work are important in this context, but
are unlikely to be the whole story among full-timers. In sum, 12–18 months out of
university, gender gaps on the intensive margin are quantitatively small and appear to
play only a minor role in explaining the observed gender pay gap. Gender gaps on the
extensive margin instead are more pronounced, and field of study turns out to be a key
proximate factor in determining such differentials. To understand more about the role
played by degree categories, we next analyze the extent of full-time gender earnings gaps
across different fields of study.

<hs>  Heterogeneity by field of study</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We look again at the four different degree subjects we have already analyzed before (Table
9). Panel A shows the estimates obtained on the sample that excludes individuals in
training and Ph.D. programs, whereas panel B includes such individuals. In interpreting
the estimates one needs to keep in mind that different subject fields have different
propensities for further training, as seen from the difference in sample sizes between
panels A and B in Table 9. The gap between male and female economics/business graduates is
insensitive to sample selection and type of specification. Just controlling for cohort and
regional dummies results in a gender gap of about 10 log points (column (a)). After all
controls are accounted for (specification (e)), the gap remains essentially unchanged and
always highly statistically significant. More variation is instead observed for the other
fields. For example, when we only condition on time and regional dummies (specification
(a)), the full-time gender earnings gap is 30 log points among STEM graduates if we
include individuals involved in training/Ph. D. programs (panel B), but it reduces to 13
log points if we exclude them (panel A). In the case of medical studies, we find a
significant pay gap of about 9 log points in panel A. Including individuals in training
and internship programs leads a much larger sample (panel B), in which however we cannot
detect any significant pay differential by gender. Similar patterns emerge in the case of
humanities, albeit with different values of the estimated gender gaps. Overall, in Panel A
the point estimates are quite similar across subjects (column (e)), even though the
estimate for humanities is not statistically significant. In Panel B, however, there is a
striking difference between Economics/Business and STEM on the one hand, with significant
gender gaps close to 12 log points, and Humanities and Medical studies on the other hand,
with an insignificant gender gap of around 2 log points. Given a large fraction of
graduates in the latter fields are involved in some sort of further training, the next
step it to see what happens to their labor incomes after its completion. This is another
area to be explored by future research.

<hs>  Public versus private sector</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Recent work by Mas and Pallais (2017) and Wiswall and Zafar (2018) suggests that there are
significant differences in male versus female valuation of non-wage benefits, and job
stability and work flexibility in particular. We investigate this point by comparing the
gender-specific probability of entering the public sector. Clearly there are many
potential differences between public and private sector jobs. Nonetheless, the additional
job security and the flexibility in terms of work-time (including the ability to adjust
between full-time and part-time as family circumstances change) is a potentially important
aspect in this context. Table A.3 shows the results, where indeed we find a striking
difference between gender. Across all subjects, females are 4 percentage points more
likely to enter the public sector than males, which is a substantial difference given the
baseline rate of about 13%. In particular, when we look at STEM subjects, females are 8
percentage points more likely to work in the public sector, compared to an overall mean of
less than 10 per cent. In our data, monthly earnings of public sector workers are
significantly lower (controlling for field of study).21 This suggests that these tradeoffs
maybe very relevant in the population we are studying. Occupational and sectoral choice
are therefore important areas for future research.

<h>DISCUSSION AND CONCLUSIONS</h>
--------------------------

We have examined gender differences in university performance and labor market outcomes
among German college graduates. A key aspect of our labor market analysis is that we have
focused on the short run, looking at gender gaps soon after graduation, thus limiting the
role played by marriage, children, career interruptions, negotiations with employers, and
promotions which many have found to put greater constraints on women’s careers than men’s.
Before 1995, more men entered college than women; but in the following 20 years, the
numbers have become roughly equal. More women than men, however, complete their degrees.
This is consistent with differential dropout rate by gender which might have consequences
on the cohorts of male and female graduates entering the labor market. In terms of
quality, female graduates enter college with slightly better high school marks,22 but
leave university with slightly lower grade levels. This again might reflect a greater
dropout rate among men. But it might also reflect other factors (such as men achieving
maturity and catching up with women in terms of academic skills, or universities offering
programs that are better suited to men’s than to women’s abilities), which deserve more
research in the future. Immediately following university completion, full-time men earn
more than full-time women, even though they have very similar weekly hours of work.
Between 12 and 18 months after leaving college, the gender gap in full-time monthly
earnings is nearly 20 log points across all graduation cohorts, if individuals in
professional training or Ph.D. programs, who are likely to be paid below market wages, are
excluded. The single most important proximate factor that explains the sizeable, early
gender gap in pay is the field of study at university. There is heterogeneity in the
magnitude of the gender pay gap by field of study, with the largest differentials emerging
among graduates from economics/business and STEM subjects. Once the full set of controls
is taken into account, the remaining wage gap is about 8 log points when we estimate
across all available cohorts. Several channels may be at work here. One could be related
to human capital considerations. The importance of field of study in our results indicates
the relevance of pre-market choices. These also interact with subsequent market decisions
(such as occupational choice) at the very beginning of professional careers (e.g., Canon
and Golan, 2017; Liu, 2016). In turn, such choices could be partly driven by gender
differences in preferences (e.g., risk aversion), self-confidence, competitiveness,
earnings expectations, and valuation of non-wage benefits (e.g., Buser et al., 2014;
Fortin, 2008; Mas and Pallais, 2017; Reuben et al., 2017; Wiswall and Zafar, 2015).
Joining some (if not all) of these drivers into one coherent analysis would be another
important area for future work. Another possible channel is related to statistical
discrimination against women, based on employers’ difficulty in distinguishing more from
less career oriented women (e.g., Gayle and Golan, 2012; Reuben et al., 2014; Thomas,
2018). Also this mechanism deserves more attention in future research.


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<ART>Economic development on a finite planet with stochastic soil degradation
========================================================================

Authors: Alexandra Brausmann, Lucas Bretschger
DOI: 10.1016/j.euroecorev.2018.06.006
Year: 2018  |  Pages: 1-19
ASJC codes: 2002, 2003
Keywords: Agriculture, Environment, Natural disasters, Soil conservation, Stochastic degradation, Uncertainty

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

World economic development is associated with growing food consumption. Agricultural land, however, suffers from over-exploitation and is subject to environmental shocks which are projected to become more severe due to climate change. We present a stochastic model of a dynamic economy where soil is an essential input and natural disasters are sizeable, multiple, and random. Expansion of economic activities raises effective soil units but contributes to an aggregate loss of soil-protective ecosystem services, which exacerbates soil degradation at the time of a shock. We provide closed-form analytical solutions and show that optimal development is characterized by a constant growth rate of stocks and consumption until an environmental shock arrives causing all variables to jump downwards. Optimal soil management consists of spending a constant fraction of output on preservation measures, which is an increasing function of the shocks hazard rate, degradation intensity of agricultural practices, and the damage intensity of environmental impact. We derive the optimal propensity to save and discuss the impact of human pressure and risk exposure on soil and output. We also discuss quantitative impacts of climate change on optimal soil management.

--------------------------------------------------------------------------------


<hs>  Soils at risk</hs>
  ~~~~~~~~~~~~~

Rising food demand and growing risks of large-scale land degradation suggest bringing back
to macroeconomics what is by now the “nearly forgotten resource” –  soil.1 It is estimated
that by 2050 agricultural production will have to rise by 70% to meet the needs of growing
world population (FAO, 2009).2 However, already nowadays about one third of all soils are
degraded and the global amount of productive land per person could in 2050 be only one-
fourth of the level in 1960, if current management practices and policies remain
unchanged.3 A moderate interpretation of U.S. President Franklin D. Roosevelt’s quote that
“A nation that destroys its soils destroys itself” would read that important aspects of
well-being like food security, human health, clean air, and clean water are at risk when
quantity and quality of world’s soils are not taken care of Wall and Six (2015). The
challenge is amplified by changing weather patterns and climate variability, which force
farmers to adopt ecosystem-unfriendly practices. This provides ample motivation to study
the consequences of endogenous stochastic land degradation for long-run development.4 Soil
cultivation raises availability and productivity of arable land but involves major risks
and uncertainties. In fact, risk is an inherent element of all agricultural activities.
The development of agriculture itself was a response to the risks of relying on hunting
and gathering for food (Hardaker et al., 2004). The impact of risk has not disappeared, of
course, but it has changed its character and has shifted to different areas. It is still
inevitable, because food markets are closely interlinked with the rest of the economy and,
in particular, because ecological systems and weather conditions are increasingly subject
to perturbations. Many developing countries experience large variations in rainfall and
are subject to frequent extremes of flooding or drought, both of which contribute to soil
erosion and land degradation (UNEP, 2015). Drought and erosion are exacerbated by poor
land management that responds inappropriately to climatic variations (UNCCD, 2009), which
are predicted to increase in frequency and severity due to climate change, increasing land
degradation even further (UNCCD, 2013). Important negative effects on soil quality arise
from the agricultural sector itself, creating potentially harmful changes in the
ecological systems supporting the farms (Lichtenberg, 2002). For example, land use
changes, irrigation, or deforestation may cause soil erosion and nutrient depletion. The
use of pesticides, animal wastes, and soil siltation may contaminate surface and ground
waters. Salinization of rivers may damage crop production in downstream areas, while
irrigation and land clearing may lead to land loss to selenium and salt drawn up from
subsoils. Degradation is often due to increased disruption of macroaggregates, reductions
in microbial biomass, and loss of labile organic matter which are induced as negative
externalities from aggregate economic activities. Under appropriate market conditions,
farmers are able to respond to risks in an optimal manner. However, institutional
deficiencies, such as incomplete land tenure systems as well as negative externalities
from individual farming on aggregate soil protection, cause suboptimal development. Also,
the lack of information about the impact of soil shocks and high individual rates of
impatience may constitute management problems for soil. Soil degradation can be addressed
by different types of corrective measures. Labrière et al. (2015) empirically estimate the
impact of contour planting, no-till farming and use of vegetative buffer strips on the
reduction of soil erosion and find enormous potentials. They conclude that the government
or natural resource managers can help decrease soil losses on a large scale. It has been
stressed in the literature that such measures can be implemented by individual farmers, by
farmer cooperations, or via public policies.5 It is often stated that human pressures on
soils are reaching critical limits, reducing and sometimes eliminating essential soil
functions (Islam and Weil, 2000). Human pressures may entail unsustainable land use and
vulnerability to land degradation, including overcultivation, overgrazing, poor irrigation
practices, deforestation, and polluting industrial activities (UNCCD, 2009).6 Food
production and security are global concerns but soil losses are especially acute in arid,
semi-arid, mountainous, or tropical regions where the lack of protection may cause
substantial deterioration in soil quality and reduction in yields. These types of
environmental problems in production and food provision and their link to general economic
development warrant a thorough investigation from a theoretical perspective.

<hs>  Model and findings</hs>
  ~~~~~~~~~~~~~~~~~~

We develop a dynamic model of an economy where investments increase the capital stock and
the effective soil stock, defined as an index of soil quantity and quality. Investments in
agricultural expansion have positive output effects but may also entail negative impacts
on soil quality. For instance, clearing and fertilizing of soils are aimed at raising land
productivity and profits but may, at the same time, harm the functioning of the ecosystem
making it more vulnerable to degradation and natural disasters such as floods, droughts,
storms, landslides, etc. The latter may typically have large economic consequences and at
the same time are not easily predictable. We therefore model such calamities as random
shocks. Our model refers to a planner internalizing such external effects in the economy.
This is a generic approach to policy, so that we do not have to specify whether the
political actors are public or private and, similarly, domestic or foreign. The paper
addresses several specific research questions. We first ask about the long-run development
prospects of an economy which is subject to endogenous stochastic soil degradation. A
second issue concerns optimal management practices and optimal public policy in the
presence of random shocks. We specifically inquire about the optimal balance between
economic expansion and protection of existing soils. Our model delivers closed-from
analytical solutions for the optimal growth rate of consumption, the gross saving
propensity, and optimal soil preservation measures. We extend the analysis to include
human stress and increasing risk exposure. Our main findings can be summarized as follows.
First, we confirm that the damage-related parameters, such as the shock hazard rate, the
extent of harmful agricultural practices, soil exposure, and damage intensity, have the
expected negative effect on the optimal consumption growth rate. Productivity naturally
fosters the optimal growth rate, while soil protection efficiency may have either a
positive or a negative effect, which we explain in detail. Soil shocks are transmitted to
the capital stock intensifying the economic downturn. Second, we show that the optimal
soil preservation consists of devoting a constant fraction of output to soil protection.
This fraction is an increasing function of the shock arrival rate, agricultural
technology, proportion of harmful by-products, exposure component, and damage intensity.
The role of each parameter is therefore identified precisely. Third, we show that the
optimal propensity to save and invest crucially depends on the elasticity of intertemporal
consumption substitution and therefore widely adopted logarithmic preferences, favored for
their simplicity and tractability, may deliver misleading policy conclusions. Fourth, as
long as agricultural labor force increases the marginal productivity of land, it also
raises the optimal growth rate of consumption and the optimal fraction of output devoted
to soil protection. Fifth, we show that higher population raises soil damages in case of a
shock, reflecting the concern of human pressure on soil. Sixth, countries with a higher
risk exposure turn out to experience a slower economic growth. Finally, we resort to the
data on worldwide soil degradation to illustrate and discuss the consequences of
increasing hazard rates of weather and ecosystem-unfriendly practices on optimal soil
protection.

<hs>  Contribution to the literature</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Starting with the seminal contribution of Dasgupta and Heal (1979), growth possibilities
in the presence of natural resource scarcity has been one of the main topics in resource
and environmental economics. Within the endogenous growth literature it has been
established that exhaustibility of natural resources may not pose a constraint on growth
when innovations are resource-saving. On the other hand, exploitation of the resource and
the associated pollution may pose environmental problems (Gradus and Smulders, 1993). In
addition, resource scarcity may disrupt social processes that support innovation (Barbier,
1999). With the recent advances in endogenous growth theory, economic development under
the restrictions of a finite planet has become again a topic in mainstream literature.
Peretto and Valente (2015) call the sustainability of development in a limited habitat
“one of the main future challenges” and investigate mechanisms linking resource
availability, income, and population, thinking of the natural resource as being “land.”
While their paper focuses on endogenous population and innovation dynamics, land input
remains fixed. This is where our paper aims to make a contribution. Our model highlights
that soil cultivation is able to increase land availability and/or land productivity even
when the surface of the planet is finite. But we also stress that soil expansion comes at
the cost of increasing the risk of land degradation triggered by environmental shocks.
According to our setup, effective soil can be expanded by agricultural investment
activities on the one hand but it is subject to stochastic and endogenous environmental
shocks on the other. In this respect, our paper also builds on the literature on optimal
environmental policies, where, for example, the negative impact of pollution on
productivity or utility is stochastic and appropriate taxation measures are warranted
(e.g. Bretschger and Vinogradova, 2017; Soretz, 2007). Many contributions in the
literature deal with the complex interplay between agriculture and ecosystem services. The
early contribution of McConnell (1983) uses soil depth and soil loss for aggregate
production to determine the difference between the private path of erosion from the
socially optimal path. Dalea and Polasky (2007) analyze the environmental impacts of
agricultural practices on a wide range of ecological services such as water nutrient
cycling, soil retention, quality, pollination, carbon sequestration, and biodiversity
conservation. They also show that ecosystem services have a positive impact on
agricultural productivity. Heal and Small (2002) study agriculture as a producer and
consumer of ecosystem services and stress that the quantity and quality of ecosystem
services depend on the joint actions of many dispersed resource users.7 Lanz et al.
(2016b) stress that the concentration on a small number of highly productive crops has led
to a significant loss of biodiversity which may have a negative feedback on agriculture.
We build on these fundamental relationships in our framework by explicitly modeling the
decrease of protective ecoservices as an externality of agricultural activity. Grepperud
(1997) extends the previous studies by analyzing time-limited effects of optimal soil
conservation measures and long-lasting effects on the soil base.8 In the study of the
tropical forest ecosystem in Bangladesh, Islam and Weil (2000) argue that “human
population pressures upon land resources have increased the need to assess impacts of land
use change on soil quality.” Our paper departs from the deterministic framework used in
these papers, introducing random environmental shocks which have been classified as
“production uncertainty” and qualified as a “quintessential feature of agricultural
production” (Moschini and Hennessy, 2001, p. 90). Most studies of dynamic soil decisions
under risk are empirical. An early exception is Hertzler (1991), who provides an overview
of the analytical tools and various exemplary applications to the field. A paper closely
related to our study is Shively (2001) which also considers a dynamic stochastic model of
soil preservation but does not provide analytical solutions to the theoretical problem.
The focus of Shively’s analysis is on the role of farm size and liquidity constraints for
the decision of subsistence-oriented households to make a one-time investment in
protective installations reducing the risk of soil erosion. Thus, the dynamics of the
investment process are not considered. His main conclusion is that public policy should
aim at enhancing saving and insurance mechanisms for small farms which are most likely to
face liquidity and subsistence constraints. Lanz et al. (2016a) introduce random shocks to
total factor productivity in agriculture and show that uncertainty requires more land to
be converted into agricultural use as a hedge against production shortages. Our paper aims
at making a theoretical contribution to the literature seeking to understand the
interactions between growth and the environment. For this purpose, we combine the
essential characteristics of soil dynamics from the agricultural literature with a
workhorse endogenous growth model from the macroeconomics literature. The key strength of
our approach is that it allows for closed-from solutions with respect to the main
variables of interest, such as preservation measures, which are of particular importance
from the policy perspective. The remainder of the paper is organized as follows. Section 2
develops our baseline framework. In Section 3, we present the main results with respect to
the optimal growth rate, soil protection, and saving propensity. Section 4 adds the
development impacts of human stress and risk exposure and presents a quantitative
application. Finally, Section 5 concludes.

<hs>  General model</hs>
  ~~~~~~~~~~~~~

Production process may involve soil management practices which are potentially harmful for
effective soil in case of an environmental event, aggravating its consequences. Put
differently, land clearing may weaken soil resilience or may result in by-products which
lead to deterioration of soil-protecting ecosystem services. We postulate that a unit of
output is accompanied by η units of harmful practices which cause damage to the ecosystem
(Clarke, 1992). Exploitation of ecosystems leads to their weakening or even exhaustion,
which in turn reduces their capacity to protect and preserve the quantity and/or the
quality of agricultural land, making the soil vulnerable to degradation.10

<hs>  Solving the model</hs>
  ~~~~~~~~~~~~~~~~~

It follows that the last term on the RHS is negative and it represents the downward jump
in consumption every time a shock occurs. The solution of the maximization problem (1)–(7)
is characterized by optimal consumption is proportional to the effective capital-soil
stock; optimal protection expenditure is a constant fraction of output; consumption,
effective soil stock, and protection services increase at the same constant rate, given by
(11), between two subsequent shocks. Provided in the appendix. □

<h>ANALYSIS OF THE SOLUTION</h>
------------------------

In this section, we provide a characterization of the optimal consumption growth and the
optimal soil protection. In particular, we are interested in the effects of the key
parameters such as exposure and damage intensities, protection efficiency, shock arrival
probability, population size and technology.

<hs>  Consumption growth</hs>
  ~~~~~~~~~~~~~~~~~~

The expression resembles the Keynes–Ramsey formula which is widely known in standard
macroeconomics. The Keynes–Ramsey growth rate is typically equal to the difference between
the real interest rate (usually the marginal productivity of physical capital) and the
rate of pure time preference, multiplied by the elasticity of intertemporal consumption
substitution (EICS). We note that in Eq. (13) the economy’s implicit real interest rate is
given by the first term inside the curly braces. It does not only include the marginal
productivity of capital-soil input (ξLβ) but also the effect of harmful agricultural
practices adjusted by the protection efficiency, i.e., the term η/ω. It follows that soil
deterioration has an unambiguously negative growth effect. This adverse effect may be
reduced by either increasing the protection efficiency, ω, or decreasing the proportion of
harmful agricultural practices, η. We will discuss the role of labor for soil development
separately in the section on “human stress” below. The responses of the consumption growth
rate to changes in the fundamental parameters of the model are summarized in Proposition
2. It is important to distinguish between the effect of the expected frequency of
disasters and the effect of the overall uncertainty. The former takes into account only
the arrival rate λ. The latter includes both the arrival rate and the damage caused by a
shock, as reflected in the last term in Eq. (13). The optimal growth rate of consumption
is a decreasing function of shock arrival rate (λ), proportion of harmful practices (η),
and exposure intensity (σ); an increasing function of the international interest rate (r)
and labor force (L); either an increasing or a decreasing function of soil protection
efficiency (ω) and damage intensity (δ), depending on the parameter constellation.
Provided in the appendix. □ The effect of the arrival rate (λ) on the optimal growth rate
is directly proportional to the negative of the elasticity of intertemporal consumption
substitution. Although there is not a general consensus on the magnitude of this
elasticity, the empirically plausible range of values lies between 1 and 3. This suggests
that if the frequency of disasters were to rise in the future due to a weakened ecosystem,
the agrarian economy may experience an important growth slowdown. The intuition behind the
effects of η and of the interest rate r is rather straightforward and has already been
discussed. The effect of the protection efficiency ω is also ambiguous. On the one hand, a
higher ω directly improves protection efficiency and contributes to soil preservation thus
enhancing the growth rate through the first term in Eq. (13). On the other hand, a higher
ω also means a lesser degradation of effective soil units and a smaller jump in
consumption rate at the time of a disaster (the jump-smoothing effect). The ratio of post-
to pre-shock marginal utilities of consumption is reduced (see Eq. (10)) and this
contributes to a growth slowdown through the last term in Eq. (13). The overall effect of
ω on g is positive when the marginal productivity of effective land units is relatively
high (i.e. the level of technology (ξ) and/or agricultural labor force (L) is relatively
high), or the extent of ecosystem-unfriendly practices (η) is relatively large or the
degradation intensity (δ) is relatively high. This suggests that economies with a
relatively high damage intensity of production and with a higher degree of vulnerability
to shocks, such as numerous agriculture-dependent developing economies, may enjoy
substantial gains in terms of their growth rates by adopting (more) efficient protective
measures. At the same time, economies with a relatively higher total factor productivity
(such as advanced economies) may also experience an improvement in the growth rate of
their agrarian sectors by enhancing their soil-protection technologies.

<hs>  Optimal soil protection</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

Expression (14) shows that an economy which is highly exposed and where damage intensity
is sizeable has to devote a larger share of output to soil protection. When the arrival
rate is lower or exposure is less pronounced, it becomes optimal to spend less effort on
soil protection in equilibrium. The following proposition summarizes the effects of the
fundamental parameters of the model on the optimal protection share. The optimal fraction
of output devoted to soil protection is: an increasing function of the event arrival rate
(λ), technology (ξ), international interest rate (r), proportion of harmful practices (η),
exposure component (σ), risk aversion (ε), and damage intensity (δ); either a decreasing
or an increasing function of protection efficiency (ω), depending on the parameter
constellation. Provided in the appendix. □ The intuition behind the results in (i) is
straightforward. A higher frequency of disasters (λ) requires more preservation measures
in order to better protect land from degradation in the event of an adverse shock. If
governments happen to misperceive the true arrival rate λ, the preservation policy would
be sub-optimal. Specifically, if the perceived λ is lower than the true one, there is too
little preservation. This might happen due to a regime switch from a low to a high shock
frequency while the general expectations, if based on past experience, lag behind. If the
intertemporal substitution elasticity is above (below) unity, the optimal protection share
is convex (concave) in the arrival rate; the response of the protection share to a change
in the arrival rate is more (less) pronounced when protection technology is more (less)
efficient and when damage intensity is relatively large (small). Provided in the appendix.
□ Provided in the appendix. □

<hs>  Saving propensity</hs>
  ~~~~~~~~~~~~~~~~~

If the EICS is above (below) unity, the optimal propensity to save is a decreasing
(increasing) function of the disaster arrival rate (λ) and proportion of harmful
agricultural practices (η); an increasing (decreasing) function of the damage intensity
(δ) and protection efficiency (ω). Provided in the appendix. □ We note that when ε
approaches unity, the derived impact of all the parameters – and most importantly those
characterizing adverse events, λ, η, and δ – are at the lower bound of the empirically
plausible impact range.

     <hss>Population pressure</hss>

        In the context of soil management, “human stress” denotes the hypothesis that an
        economy with growing population and expanding activities causes more intensive
        land use, faster soil degradation, and hence a sharper destruction of protecting
        ecosystem services. Reviewing the data and the literature, Eswaran et al. (2001,
        p. 7) conclude that a high population density in an area that is highly vulnerable
        to desertification poses “a very high risk for further land degradation.” In our
        model we have derived the joint development of a country’s capital and soil
        stocks. Economic expansion involves both increasing capital and soil use causing
        higher soil damages when a shock occurs, see Eq. (4). Population size has also a
        major effect in our economy.19 An increase in labor (dL > 0) raises the
        productivity of each capital-soil unit which results in a higher consumption
        growth. The result is an example of the so-called “scale effect” of growth which
        is a consequence of the constant returns to capital. It says that a larger
        population can exploit higher capital stock more efficiently which is favorable
        for growth. The empirical validation of the scale effect has been challenged in
        the literature, see Jones (1995). As a response to the critique and focusing on
        market structure, Peretto and Smulders (2002) show how an innovation-driven
        economy achieves endogenous growth without a scale effect. Specific to our
        contribution is that population size induces not only a growth effect but, at the
        same time, a negative damage effect. Indeed, following Eq. (4), the marginal
        damage as a side-product of soil investments grows with labor input (because labor
        is an argument in the production function). With the emergence of non-monotonic
        growth our model adds a new perspective on the scale effect and is not directly
        subject to the earlier critique about its consequences. The impact of population
        size on damage size addresses the often-stated concern about improper soil
        management in a situation of human stress.

     <hss>Population dynamics</hss>

        An interesting question is what would happen in our model if population size were
        fully endogenized. It is clear that such an analysis requires a different model
        setup and, in particular, a decentralized economy where households are allowed to
        make fertility decisions. A model of this type is elegantly presented in Peretto
        and Valente (2015). We note that, differently from our initial setup, their model
        includes in particular (i) a more sophisticated production sector and (ii) a
        constant endowment of a non-exhaustible resource. Since we do not study the effect
        of population size on innovation, we abstract from (i) and think of the simple
        production structure as in our Eq. (6). Our model adds in relation to point (ii),
        namely we endogenize the dynamics of resource, S. It is important at this stage to
        define how households perceive their impact on S. If they do not internalize the
        negative effect through damages to ecosystem, then they do not invest anything in
        protective measures and some policy is required to correct for the externality. In
        this case, and without appropriate policy intervention, it is clear that per-
        capita consumption will converge to zero in the long run. On the other hand, if
        households do internalize the externality, at least to some extent, their
        fertility decision will take into account the “human stress” effect on ecosystem
        and will result in a lower equilibrium fertility rate, as compared to the case
        without internalization, or even in a stabilization of population at a constant
        level. The latter case would correspond to our initial framework. In the former
        case, we conjecture, the endogenous fertility rate is closely related to the
        stochastic growth rate of S: assuming that a household size can adjust
        instantaneously, the population size increases at a constant rate in between
        shocks and drops when a shock occurs as households immediately respond to the
        scarcity of S.

<hs>  Risk exposure</hs>
  ~~~~~~~~~~~~~

To provide empirical evidence we may note that Africa is particularly vulnerable to land
degradation and desertification (UNEP, 2015). Moreover, it is the poorest of the
continents with a disproportionate share of low-income countries compared to other world
regions and a very low level of economic development. The Economic Commission for Africa
reported that in 2013 Africa’s share of the world population was 13%, but its share of
global GDP was only 1.6%. Comparing the different countries within the continent it is
striking that many poor economies, in particular Burundi, DR Congo, R Congo, Gabon,
Liberia, Sierra Leone and Zambia have a very high percentage of degraded land (UNEP, 2015,
pp. 123–130), supporting our hypothesis of soil damages and land degradation negatively
affecting economic development.20 The result also makes clear that a growing arrival
frequency in the future, e.g. induced by climate change, will deepen the income gap
between the vulnerable countries of the South and the less vulnerable economies of the
North, which acts against the sustainable development goals. Even if deficiencies in
markets and policy of the South were absent, this would indicate a need for support of the
South. Realistically assuming that market failures and weak institutions in less developed
countries entail higher soil mismanagement, specific policy to correct for externalities
and to strengthen institutions has to be implemented to improve welfare and development
conditions in the South.21

<hs>  Quantitative analysis</hs>
  ~~~~~~~~~~~~~~~~~~~~~

In this section we attempt to quantify our theoretical predictions, in spite of the fact
that reliable numbers for soil degradation and its economic impact are rather difficult to
obtain. Soil degradation has different dimensions, such as soil loss, sealing,
contamination, acidification, salinization, compaction, and nutrient decline, which are
not directly comparable. Moreover, the situation differs depending on climatic conditions,
e.g. in arid regions vs. rain forests. Gibbs and Salmon (2015) report global estimates of
total degraded area varying from less than 1 billion ha to over 6 billion ha, with equally
wide disagreement in their spatial distribution. Eswaran et al. (2001) state average
estimates for all degraded lands as percentage of total land for the continents: Africa
73%, Asia 71%, Europe 65%, and South America 73%. Lal (2001, p. 531) reports production
losses due to soil erosion in Africa between 2% and 40% with a mean loss for the whole
continent of 9% which could rise to 16.5% by 2020. Soil erosion is by no means restricted
to developing countries, it is also important in Europe and the U.S. The study of Kuhlman
et al. (2010, p. 27) concludes that soil erosion by water and wind causes an average
productivity loss per hectare in Europe of 0.16% per year. It is calculated that an
effective soil erosion control programme in the EU would provide annual on-site benefits
of 500 million Euros over a 20-year period equivalent to a present value of 3.25 billion
euros. Comparing the figure to the costs of the programme supports our model hypothesis of
external effects, motivating the need for public policy: the on-site benefits for reducing
erosion on agricultural land turn out to be smaller than their costs, while adding the
off-site benefits shows significants improvement in social welfare when implementing the
programme. The need for public soil protection policy depends on the size of market
failure in soil management. Den Biggelaar et al. (2003, p. 2) conclude: “Comparing the
results of past and present erosion studies indicates that inappropriate soil management
may amplify the effect of erosion on productivity by one or several orders of magnitude.”
An important case for externalities is the use of water. It is reported that the common
water resources are rarely used efficiently and that “environmental externalities have
arisen through excessive utilization of non-recharged aquifers while, in a number of
cases, the excessive application of irrigation water has resulted in rising groundwater
tables, soil salinization and sodification problems” FAO (2015, p. 402). Even though the
parameters of our model are not straightforward to calibrate under these preconditions we
can provide some rough measures for the expected effects of accelerating climate change.
We remain very cautious about choosing parameter values and limit the analysis to the
impact of a few key factors on optimal soil protection. One such important factor is the
frequency of natural disasters, which is predicted to increase over time due to rising
global mean temperature (IPCC, 2014; Thomas and Lopez, 2015). For instance, the number of
meteorological disasters has risen from about 25 per year to over a hundred during the
period 1970–2014. Similarly, the number of hydrological events has risen from about 80 to
almost 150 over the same time frame (Thomas and Lopez, 2015, Fig. 1). At the same time,
exposure, defined as the presence of people, livelihoods, ecosystems, environmental
services, resources, etc., has also increased due to societal change. IPCC (2012)
documents that fatality rates and economic impact, e.g. losses as a proportion of gross
domestic product (GDP), are higher in developing countries due to higher share of
impoverished populations, weak infrastructure, lack of basic facilities, and limited
government capacity. Residents of the developing economies are not only more vulnerable to
natural disasters but at the same time they have less resources for management options and
fewer coping strategies. Therefore, soil degradation and food security in general are more
acute issues in those regions. When choosing parameters for calibration we shall restrict
our attention mostly to those pertaining to the developing world. In addition to disaster
frequencies, ecosystem-exploitative practices have also risen over time – across the globe
but mostly in the developing world (e.g., shrinking of the Amazonian rainforest). We
therefore consider next the effects of η and ω on the optimal preservation measures. To do
so, we use again the study of UNEP (2015) which relies on the well-established WOCAT
(World Overview on Conservation Approaches and Technologies) database. For the 42 African
countries, the study concludes that the loss of about 105 million hectares of croplands
can be prevented provided that soil erosion is managed appropriately (UNEP, 2015, p. 11).
The estimation of crop losses in terms of economic value involves an econometric
estimation of the loss of ecosystem services and of the marginal physical product of
different environmental variables as well as the use of market prices (UNEP, 2015, p. 58).
With the already-mentioned cost of land degradation of about 286 billion PPP USD each
year, the costs of inaction against land degradation in Africa turn out to be very high.
Conversely, implementing better soil practices is found to be much less expensive.
Specifically, expenditures for sustainable land management practices were calculated to
cause an annual cost of about 9.4 billion USD or 1.15 % of the GDP (UNEP, 2015, p. 91).
Protection efficiency, ω, may be raised by adopting more technologically-efficient
equipment and techniques, as well as by applying fertilizers with high-nutrient content.
We recall from our discussion of Proposition 3 that the impact of ω on q* is ambiguous,
because ω affects the leverage of the policy, the growth rate, and the downward jump in
case of a shock. Using our calibrated parameter values we find that a 10% increase in
protection efficiency leads to 0.1 percentage point decline in the optimal protection
share, i.e. q* falls to 1.05%. In addition to the effects of rising hazard rates of
climate shocks, ecosystem deterioration and changes in technological efficiency, one may
be interested in the long-term projections of expenditure on soil preservation. Such
projections can be useful for government budget planning when financial priorities may be
shifting in light of changing climatic conditions and additional investment projects need
to be undertaken. If we remain in the context of the African economies and, more
specifically, the most vulnerable region of Sub-Saharan Africa, we may ask ourselves how
much this region should spend on agricultural policies aimed at soil protection over the
next 30 years. Such a projection undoubtedly depends on the region’s future growth rate.
The World Bank data indicate that the average GDP growth rate in the region reached 1.2%
and was −1.5% on a per capita basis. We shall assume for simplicity that the economies of
this region will have a zero average growth rate in the next 30 years. We also posit that
the protection spending derived from UNEP (2015) of 1.15% of GDP is optimal under current
climate conditions. Depending on the assumptions about shock’s hazard rates and
coefficient of relative risk aversion, we obtain the following projections for expenditure
on soil preservation measures: As an alternative to the analysis of aggregate soil
functions and overall economic linkages one may resort to the study of subsystems like
soil organic carbon (SOC) which reveals some interesting characteristics of soil
degradation. It has been shown that conventional agriculture leads to a loss of about
fifty percent of SOC over a period of 20–30 years (Petersen and Hoyle, 2016). Conversely,
increasing SOC by using alternative soil management practices is beneficial to soil
functions, fertility, and buffering capacity. However, the benefits of alternative land
policies strongly vary with soil quality. For example, in areas with low rainfall and
sandy soils like in Western Australia, productivity improvement in agriculture is much
less important compared to the sequestration value for climate policy when increasing SOC,
see the numbers in Petersen and Hoyle (2016). As a consequence, the benefits of altered
soil management heavily depend on the used carbon price an thus on the adopted climate
policy, which is beyond the scope of the present paper. The analysis of other specific
soil functions or of specific countries and regions reveals that the degree of
heterogeneity is still considerable on a less aggregate level, especially when the
economic valuation is a focus. Hence, different calculations and specific considerations
would be needed for each of the many different cases. To concentrate on the main messages
for the economics of soil degradation, we have restricted the analysis in this paper to
the aggregate approach to soil degradation and protective policies, both in theory and the
quantitative implications.

<h>CONCLUSIONS</h>
-----------

The present paper considers an economy which produces output employing three essential
inputs: capital, soil and labor. Production process, accompanied by harmful agricultural
practices, weakens the ecosystem and diminishes its protective services. The soils become
vulnerable to random environmental shocks which lead to soil degradation. Such a scenario
is observed in numerous developing countries with large agricultural sectors. In an
attempt to raise yields and profits, farmers clear a slot to gain arable land but at the
same time they lose the protective ecosystem services and make their land exposed to
landslides, floods, droughts, winds and similar calamities. To ensure sustained yields, it
thus becomes necessary to adopt soil preservation measures (e.g. installation of contour
hedgerows to prevent landslides). Since the extent of soil degradation depends positively
on the magnitude of harmful agricultural activities and negatively on the protection
efforts, an optimal soil expansion and preservation policy can be designed to maximize the
economy’s expected lifetime welfare. In the present article we provide a clear-cut closed-
form solution to this dynamic stochastic problem. The optimal development of the economy
is characterized by capital and soil stocks and the consumption rate which all grow at the
same constant rate until a disaster occurs causing a downward jump in all variables. In
the benchmark model we assume that shocks arrive at a constant Poisson rate. The
percentage reduction in consumption, i.e. the size of the jump, is constant and depends on
the arrival rate, the damage intensity, the protection efficiency and the intertemporal
substitution elasticity (EICS). The optimal soil preservation strategy consists of
devoting a constant fraction of output to protection measures. This fraction is an
increasing function of the hazard rate, the damage intensity, the level of agricultural
technology and agricultural labor force. It may be either increasing or decreasing in the
protection efficiency due to three counteracting forces, the direct effect, the jump
effect and the growth effect. The EICS appears to play a crucial role in determining how
the economy’s propensity to save responds to changes in the key parameters, including
those characterizing adverse shocks. For a relatively high value of EICS (above unity), we
find that an increase in disaster frequency leads to a decline in the saving propensity,
implying that soil conservation measures and current consumption increase at the expense
of capital-soil stock expansion. An increase in the damage intensity of shocks leads to an
increase in both protection measures and saving propensity. Consequently, an increase in
the disaster frequency and in the damage intensity, while both having a positive impact on
preservation measures, have diverging effects on the propensity to save and thus on how
consumption possibilities are spread over time. Population size has a positive effect on
growth but intensifies negative soil shocks. Finally, a high soil risk exposure causes a
lower economic growth, even when capital markets are fully integrated and the world
interest rate is given. Soil conservation has recently reemerged as an important issue in
policy debate, especially for world food security and for developing economies where a
significant share of population still relies on agriculture for subsistence. The present
article provides a theoretical foundation for the analysis of optimal growth and for the
formulation of management and policy prescriptions with respect to soil expansion and
preservation nexus.


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<ART>Empty homes, longer commutes: The unintended consequences of more restrictive local planning
================================================================================

Authors: Paul Cheshire, Christian A.L. Hilber, Hans R.A. Koster
DOI: 10.1016/j.jpubeco.2017.12.006
Year: 2018  |  Pages: 126-151
ASJC codes: 2002, 2003
Keywords: Housing supply constraints, Land use regulation, Residential vacancy rates

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We investigate the impact of land use regulation on housing vacancy rates. Using a 30-year panel dataset on land use regulation for 350 English Local Authorities (LAs) and addressing potential reverse causation and other endogeneity concerns, we find that tighter local planning constraints increase local housing vacancy rates: a one standard deviation increase in restrictiveness causes the local vacancy rate to increase by 0.9 percentage points (23%). The same increase in local restrictiveness also causes a 6.1% rise in commuting distances. The results underline the interdependence of local housing and Labour markets and the unintended adverse impact of more restrictive planning policies.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

To an economist it might seem self-evident that vacancies in the housing stock are a
natural feature of how any market must work. There even are ‘uneaten’ apples in a well-
functioning fruit market. The Labour market is very much more comparable to the housing
market and virtually all mainstream economists expect to observe at least frictional
unemployment when the Labour market is in equilibrium (see Pissarides, 1985; Mortensen and
Pissarides, 1994; Pissarides, 1994). It is the same in any normally functioning housing
market. In equilibrium there must be vacant houses as people move and ‘house-hunt’, as
people die or houses wait to be demolished and sellers wait to find a buyer (Han and
Strange, 2015). But this view is often not shared by those who design buildings and
influence urban policy or with those who plan housing supply – at least in England. Even
in what was then one of the least restrictive English Regions, the East Midlands, in
calculating how much land should be allocated for housing to meet their estimate of their
region's ‘housing needs’, planners argued that they could allocate less land because they
assumed they would reduce the number of vacant homes: ‘The annual average housing
provision reflects a number of factors, transactional vacancies in new stock (about 2%)
add 7,000 to the requirement, but offset against that is an assumption that vacancies in
the existing stock should be reduced by a half per-cent, which will bring 8,600 dwellings
back into use.’ (Government Office for the East Midlands, 2005, Appendix 4, p. 91). It is
surely true that using ones stock of capital more intensively is a way of increasing
efficiency. That is just how cut price airlines operate: they keep their seats full and
their aircraft in the air. They, however, had an analysis of how to achieve this. They did
not just assume planes would spend more of their lives in the air and seats would be
fuller. Unless we understand why houses are vacant we cannot rationally hope to reduce the
number of vacant houses just by being more restrictive. To help improve our understanding
of the factors which determine vacancy rates in the housing market, this paper
investigates the causal, albeit reduced-form, impact of regulatory restrictiveness.
Moreover, since housing and Labour markets are interdependent, we also investigate the
related issue of how local regulatory restrictiveness affects the average commute distance
of those working in the jurisdiction. These are not the only outcomes of greater
regulatory restrictiveness. We find that there are other measurable effects apart from
raised house prices, all apparently responses to poorer housing market matching (discussed
below); more households are in temporary homes, crowding is greater, and in-migration
lower. These results stem from the insight that policy imposed restrictions on housing
supply may have two opposing effects.1 The first of these we call the ‘opportunity cost
effect’. Tighter restrictions on supply imply fewer available houses and therefore more
demand pressure for existing homes, increasing house prices and thus the opportunity cost
of keeping housing empty. This will lead to a lower vacancy rate all else equal. If this
‘opportunity cost effect’ was the only effect at work, tighter supply constraints should
unambiguously lower vacancy rates. There is however a second effect, which we refer to as
the ‘mismatch effect’. Tighter supply constraints not only reduce supply of new houses but
also influence the composition and adaptability of the bundle of attributes of both the
existing housing stock and those of new built homes. Over time the structure of
households' demand for housing attributes changes because incomes rise, the demographic
structure of the population changes and preferences themselves may change. For example, as
real incomes rise, so does the demand for certain attributes depending on the varying
income elasticity of demand for them.2 In addition there may be demographic changes such
as an increase in the proportion of single adults, which mean that market preferences
change. If the attributes of the housing stock, as a consequence of planning constraints,
cannot, or can only more slowly adjust to these changes on the demand side, matching the
demand for housing attributes with the supply of those available will inevitably become
more difficult. Hence, in line with Wheaton (1990), mismatched households may have to stay
longer in a less restrictive housing market while searching in a more restrictive one,
implying a relatively lower vacancy rate in the less restrictive market and a higher
vacancy rate in the more restrictive one. Mismatched households may also take temporary
accommodation and search for longer in more restrictive markets or have to search further
afield for a suitable home; they become mismatched on the locational characteristics of
houses implying longer commutes. Our aim in this paper is to determine the net effect of
these two opposing forces – the opportunity cost effect versus the mismatch effect – in
order to identify the role that regulatory restrictiveness plays in determining the
vacancy rate in local housing markets. To do so, we analyse panel data on housing
vacancies from 1981 to 2011 for 350 English Local Authorities (LAs), the basic local
jurisdictional unit that implements planning policies and approves or rejects individual
planning applications. One key concern in this analysis is the endogeneity of local
planning restrictiveness. The stylised fact that policy makers and local planners may
respond to higher vacancy rates by restricting supply suggests possible reverse causation.
Regulatory constraints may also be endogenous to unobserved demand factors (Hilber and
Robert-Nicoud, 2013; Davidoff, 2016) and those demand factors may directly affect vacancy
rates. To account for possible reverse causation and omitted variable bias and thus
identify the causal effect of regulatory restrictiveness, we employ an instrumental
variable strategy by exploiting specific features of the British voting system which
induces a substantial ‘randomness’ of seats won (or lost) beyond the vote share. That is,
we use the share of Labour seats in LAs, controlling for the share of Labour votes in a
flexible way, as an instrumental variable to identify local planning restrictiveness. One
could query this identification strategy because, for example, the political composition
of an LA could influence local government expenditures and those, in turn, might influence
house prices and vacancy rates. Based on a series of placebo regressions, we show that
these alternative explanations do not plausibly invalidate the main conclusions. Our two
key empirical findings are as follows. First, when we naively look at cross-sectional
data, we find a negative relationship between more restrictive local planning and local
vacancy rates, superficially appearing to confirm “planners' assumptions”. However, when
we (i) use first differencing and so control for time-invariant unobservable
characteristics, (ii) properly account for the endogeneity of restrictiveness by
instrumenting for it and (iii) control for other relevant factors, more restrictive places
have a significantly – and substantially – higher vacancy rate. That is, the underlying
causal relationship appears to be exactly the opposite to that which planners assume.
Based on our most rigorous empirical specification, a one standard deviation increase in
local regulatory restrictiveness causes the average local vacancy rate to increase by
about 0.9 percentage points (23%). Second, we find that regulation-induced mismatch has
spatial implications for Labour markets. Workers with jobs in LAs with more restrictive
planning have to search for housing they can afford and match their preferences further
afield; so they are more likely to be locationally mismatched and have to commute further.
Using a similar approach to that used for investigating the underlying relationship
between the vacancy rate and restrictiveness we find that a one standard deviation
increase in local regulatory restrictiveness causes an increase in average commuting
distance of some 6.1%. We also provide additional suggestive evidence relating to other
proxies for mismatch, such as the share of crowded or non-permanent properties and the
share of migrants. Our findings, therefore, strongly suggest that tighter local planning
restrictiveness not only leads to less efficient housing market matching but also this
effect dominates the opportunity cost effect, resulting in higher local vacancy rates
overall and longer average commutes. Hence, local efforts to reduce the number of vacant
homes by imposing supply restrictions have three unintended effects: they increase the
local vacancy rate and they increase the average commuting distance of those who work in
the jurisdiction – thereby causing a welfare cost. In addition, as the literature shows,
they increase local house prices (see e.g. Cheshire and Sheppard, 2002; Glaeser and
Gyourko, 2003; Hilber and Vermeulen, 2016). We proceed as follows. In the next section we
discuss in more depth the link between land use regulation and mismatch in the housing
market and how that affects the local vacancy rate and the average commuting distance. We
then describe our data and set out our main results. The final section draws conclusions.

<h>LAND USE REGULATION, HOUSING MARKET SEARCH AND VACANT HOUSING</h>
-------------------------------------------------------------

The price of housing services is a function of both demand and supply in the relevant
local markets. Various empirical studies document a positive effect of regulatory
restrictiveness on house prices (Cheshire and Sheppard, 2002; Glaeser and Gyourko, 2003;
Glaeser et al., 2005a, 2005b; Quigley and Raphael, 2005; Ihlanfeldt, 2007; Hilber and
Vermeulen, 2016). What these studies do not consider is the fact that, on the seller's
side, it takes time to sell a house and, on the buyer's side, search for a new house is
costly too. These search frictions lead to housing vacancies (Merlo and Ortalo-Magné,
2004; Han and Strange, 2015). It has been documented – and our data also suggest – that
housing vacancies are not constant across space and time and depend on the characteristics
and preferences of households living in a housing market, as well as on those of the
location such as characteristics that are systematic of persistently weak housing demand
(Rosen and Smith, 1983; Gabriel and Nothaft, 1988; Gabriel and Nothaft, 2001; Deng et al.,
2003; Molloy, 2016). However, the impact of land use restrictions on housing vacancies has
not yet been studied. In the context of this paper we use data on local jurisdictions – in
Britain, LAs – which we refer to as local housing markets.3 On the demand side, households
often search in a local housing market while still living in another local market, for
example due to changes in where they work (Mulalic et al., 2014; Koster and Van Ommeren,
2017). On the supply side, the characteristics of housing are the result of both the
characteristics of new build housing and the adaptation of the characteristics of the
existing stock. The degree of regulatory restrictiveness influences the characteristics of
new construction and of the existing stock in very great detail. Both new construction and
significant changes to the characteristics of existing houses – converting loft to living
space, for example – likely require ‘development control’ permission. This is the
responsibility of the LA's Planning Committee made up of locally elected politicians. This
decision making process tends to be politicised and unlike a Zoning or Master Planning
system, such as in force in the US or in most of Continental Europe, decisions are not
very predictable. As noted in the introduction, planning induced housing supply
restrictions will have two opposing effects on the housing vacancy rate: an ‘opportunity
cost effect’ and a ‘mismatch effect’. The opportunity cost effect works via restrictions
of supply reducing the availability of land for development (see for example Cheshire and
Sheppard, 2005, or Hilber and Vermeulen, 2016). This reduces the rate of new building and
so over time the size of the stock of housing relative to demand within the market. This,
all else equal, increases prices and thus the opportunity cost of keeping housing vacant.
The effect of this is unambiguously to reduce vacancy rates. It will also be likely to
increase price volatility. However, more restrictive planning policies will also change
the bundle of attributes on offer and, other things equal, slow the rate of adaptation of
housing characteristics to changes in the structure of demand with respect to them – the
mismatch effect. The latter effect is expected to increase vacancy rates. This will come
about via two separate forces, one working on the characteristics of new build and the
other on the adaptation of the characteristics of the existing stock of houses. The first
force may imply that new build houses become smaller, more distant from jobs and are more
likely to be in the form of flats or terraced houses, because there is less land available
for dwellings. The second force arises because the structure of demand for housing
characteristics changes over time and to accommodate this, the characteristics of the
existing stock of housing need to be constantly adjusted. For example, entry to the best
state schools in Britain is determined by the exact location of houses. As the relative
standing of different schools changes over time, people seeking to ‘buy’ entry to better
state schools will want more bedroom space in the best schools' catchment areas. However,
the more restrictive is the LA, the more difficult it will be to adapt existing houses to
provide more space or for developers to build additional family housing near better
schools. Another example is that as more cars have been bought (car ownership has
increased 13-fold since the current form of land use planning in England was introduced in
1947 and doubled since our vacancy data starts in 1981, Department of Transport, 2013),
the demand for garages and off street parking has increased. Such examples of ways in
which the demand for housing attributes changes over time could be increased almost
indefinitely. However, what it means is that if the supply and demand for the structural
characteristics of housing are to be efficiently matched to each other, there will need to
be constant adaptation of the characteristics of the existing stock of houses. So more
restrictive LAs will slow the adaptation of the existing stock to (changes in) the
structure of demand for housing attributes. Over time, in more restrictive LAs the
characteristics of new and existing housing available will be less adapted to preferences
of households. Hence, other things equal, if people have a (strong) idiosyncratic
preference for locations and house type (e.g. a double-earner household with children that
needs at least two-bedrooms and garden space), they will spend more time searching for
housing that matches their preferences. When households live in a less restrictive housing
market while searching in the more restrictive local market, this will imply a decrease in
the vacancy rate in the former and an increase in the latter housing market.4 In other
words, given idiosyncratic preferences, households stay longer in the ‘wrong’ places. This
may imply that younger people live longer with their parents in ‘crowded’ properties, or
that households are induced to stay in temporary accommodation while searching. Because
the housing stock does not match their current preferences, this implies a higher vacancy
rate, other things equal, in the more restrictive housing market. We provide some evidence
on some of these different symptoms of mismatch in Section 3.6 where we look at how
regulation influences the share of non-permanent homes and ‘crowded’ properties. We
discuss also a more obvious measure of mismatch in Section 3.4: commuting distances from
the workplace in the LA. We do indeed find that for workers in more restrictive LAs
commuting distances increase significantly. This result is consistent with house hunters
finding it more difficult to match their preferences in more restrictive local housing
markets so becoming ‘mismatched’ locationally. This has interesting implications for the
boundaries of local Labour markets – they appear to be determined not just by transport
costs but also by local planning policies – and how these affect the total supply of
housing and the supply of individual housing characteristics. Because households may
decide not to move to the desired more restricted place, the share of in-migrants is
expected to be lower in the more restrictive housing market. We provide evidence for the
latter in Section 3.6. The well-documented fact that tighter local regulation leads to
higher prices is indicative that the opportunity cost effect may be important in
determining local vacancy rates. However, we lack evidence on the importance of the
offsetting mismatch effect. Thus the net effect of local regulatory restrictiveness on
local vacancy rates is ambiguous. The empirical analysis that follows aims to identify
this net effect while eliminating alternative explanations. One may question whether
changes in vacancy rates are a sufficient statistic when one is interested in the welfare
effects of land use regulation. We do not argue that vacancy rates in general are a
sufficient statistic. However, when one is specifically interested in the change in
welfare due to an increase in mismatch caused by more restrictive local planning, an
increase in the vacancy rate (beyond the natural rate) is a sufficient statistic for the
former. In line with a large Labour market literature on matching, and as demonstrated by
Koster and Van Ommeren (2017), from a welfare perspective housing search may be either too
low or too high. However, when search is too low, that is caused by an externality for
sellers: if buyers search more they will find a suitable property sooner, thereby reducing
the time on the market and the associated costs for the seller. Buyers do not take this
into account when increasing search effort. However, a regulation-induced increase in
vacancy rates while increasing search effort, neither reduces sales times, nor increases
matching quality, so the welfare effects are unambiguously negative. This is important
because planning policies that aim to reduce vacancies by reducing new construction but
end up leaving more houses empty, cause an under-utilisation of a major capital asset.
According to ONS by the end of 2013 houses accounted for 61% of the UK's net worth: up
from 48.7% 20 years previously (ONS, 2016). So the capital stock represented by housing is
very significant indeed and so its underutilisation represents a significant economic
inefficiency. The effects on commuting are important in their own right as again they
represent a welfare loss resulting from increased difficulty of matching. Of course
planning policies per se have the potential to increase social welfare via correcting
market failures and we are not claiming here that our evidence on the effect of land use
regulation on vacancy rates and commuting distances in isolation suggests that local
planning restrictions reduce net welfare. However, there is evidence at least for the UK
and the US that an increase in the restrictiveness of planning policy (from current
levels) has a net negative effect on welfare (see Cheshire and Sheppard, 2002 for the UK
and Turner et al. (2014) for the US). In this context, our finding that more restrictive
local planning increases the local vacancy rate and commuting distance via raising
mismatch in the local housing market, adds to the alleged net negative effect on welfare.
Both effects (on vacancy rates and commuting distances) have been ignored in the
literature so far.

<hs>  Data and descriptive statistics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our data come from several sources. The vacancy rates are from the UK Census for the years
1981, 1991, 2001 and 2011.5 For the first three Census years we have information on the
number of vacant dwellings and we are able to distinguish between primary dwellings and
second homes.6 The 2011 Census reported only information on the number of unoccupied
dwellings including second homes. To estimate vacancies for 2011 in the most consistent
way possible, therefore, we assume that the share of second homes remained constant
between 2001 and 2011. In a robustness check we use an alternative dataset for vacancy
rates (available for 2001 and 2011 only) to test whether our findings are sensitive to
this adjustment. The latter dataset is provided by the Department of Communities and Local
Government (DCLG) using the LA returns for the Council Tax.7 Our measures of regulatory
restrictiveness come from the DCLG's Planning Statistics. Following the literature, our
key measure is the refusal rate for major residential projects available for each LA on an
annual basis. The refusal rate for ‘major’ projects is defined as the share of
applications for residential developments of ten or more dwellings that is refused by an
LA in any year during the process of ‘development control’. We calculate this for each LA
using data on all applications and refused applications of major developments for the
Census year itself plus the two years preceding it.8 In what follows we call this variable
the refusal rate. As a proxy for local (housing) demand we use LA-level male weekly
earnings for the period from 1981 to 2011. Our earnings data come from the Annual Survey
of Hours and Earnings (ASHE) for 2001 and 2011 and from the New Earnings Survey (NES) for
1981 and 1991. We obtained the ASHE data at the LA-level but the NES data for earlier
years are only available at the county and London borough level. We then geographically
matched all earnings data to the LA-level and deflated the nominal earnings figures by the
Retail Price Index to obtain real earnings. For more details on the data and procedures
used, see Hilber and Vermeulen (2016). A number of other factors may influence vacancy
rates, in particular housing tenure, demographics and socio economic characteristics. We
obtain these control variables from the Population Censuses. Our list of controls includes
the local homeownership rate. Homeowners tend to move less often than renters, and this is
likely to be reflected in higher vacancy rates for rental housing. We also control for the
share of council housing. Because rents of council houses are usually below market value,
there are waiting lists for them. This is likely to imply a shorter duration of vacancies
(Pawson and Kintrea, 2002). However, this effect could be offset to the extent councils
have less efficient housing management. The Population Censuses also provide data on the
share of people between 30 and 64 and the share of elderly, 65 and over. Young people may
be more flexible in their housing choices than older people, and they may be less
selective because they are more income constrained or have lower search costs (perhaps
because of lower opportunity costs of time) leading to lower vacancy rates in LAs where
there are proportionately more young adults. On the other hand, younger people tend to
have a higher mobility rate, leading to higher vacancy rates. The mortality rate is of
course highly correlated to the share of elderly. Death frequently implies that houses
become vacant and, moreover, because of probate and perhaps other reasons (the new owner
may not be a local resident or the house has suffered a period of neglect so is more
likely to need refurbishment) houses that become vacant on the death of their owner are
likely to remain vacant for longer. Other control variables derived from the Population
Censuses are the share unemployed, the share of highly educated, and the share of
residents with permanent illnesses. As a proxy for mismatch and as a significant focus of
interest in its own right, we gather data on the average commuting distance from the
workplace for all the Census years. The data provide us with the share of people per
commuting distance band (0–2 km, 2–5 km, etc.). We then calculate the average commuting
distance by taking the midpoint of each category and weighting it by the number of persons
in each category. We further gather data on other variables that may relate to spatial
mismatch from the Census, such as the share of crowded properties, the share of shared
properties, the share of migrants and the share of non-permanent dwellings. Our
instrumental variable strategy employs information on the political composition of the LA
and local vote shares. We obtained the local election data from various sources: (i) the
British Local Election Database (1889–2003) compiled by Rallings and Thrasher (2004), (ii)
the Local Election Handbooks (1999 to 2008), (iii) the Local Elections Archive Project
(LEAP) (2006 to 2010) and (iv) the BBC (2009 to 2011). We do not have data on four LAs, so
these are excluded from the analysis, leaving us with a sample of 350 LAs and four Census
years (1981, 1991, 2001 and 2011).9 Since it might be argued that turnout is
unrepresentatively low at local elections in the sensitivity analysis, we also use data on
general elections, by matching each Census year to the nearest general election year
(i.e., 1983, 1992, 2001 and 2010). The LA-level share of votes for the Labour party in the
general elections is derived from the British Election Studies Information System. For
more information on the election data, see Appendix 1. We also gather data on net local
expenditures from the Chartered Institute for Public Finance and Accountancy (CIPFA)
annual reports on finance and general estimates available for each LA. We choose spending
categories that remain robust over time, such as spending on education, personal and
social services (such as social care), highways, housing services, local planning and the
total local net expenditures. Because these are net expenditures, they may be negative in
certain instances. We express the local expenditures in £ per head of the population. We
note that for education, personal and social services, and highways, the largest share of
the spending is done at the county level. Although LAs have some freedom to spend extra
money, we add the net spending per head at the county level to the local expenditures in
these categories (otherwise most values would be zero). This also explains why the total
local expenditures of an LA are lower than, for example, the net spending on education:
the total expenditures only refer to expenditures by the LA itself. In a few instances
data are missing for individual LAs (in particular for a dozen LAs in Greater London in
1981). In cases such as this we impute the missing values from the average spending in a
county, implying (a small) measurement error. However, in the placebo regressions in
Section 3.4 the spending is the dependent variable. As long as this measurement error is
random, it does not affect the estimated coefficients. We obtained data on house prices
from the Land Registry (1995–2011) and the Council of Mortgage Lenders (CML) (1974–1995).
We do so by taking account of the composition of sales in terms of housing types by
adopting a mix-adjustment approach (see Wall, 1998). The real price index is obtained by
again deflating the nominal series with the Retail Price Index. We then use the price
index to create a measure of local price volatility; for more information see Hilber and
Vermeulen (2016). Table 1 presents the descriptive statistics. The average overall vacancy
rate is about 4%. The vacancy rate in 2011 was 3.6%. This is only slightly lower than in
the United States, where it was 4.5% in 2012. This might seem surprising when one takes
into account the enormous excess supply of housing in the wake of the Great Recession that
made housing extremely affordable in the US. In Fig. 1 we plot the cross-sectional
relationship between the vacancy rate and house prices. Vacancy rates are somewhat lower
in areas with high prices (ρ = − 0.246), consistent with the opportunity cost argument
discussed above. There is little response to the housing market cycle; the correlation
between the change in the vacancy rate and the change in house prices is very low with ρ =
− 0.069. We map the average local vacancy rates over the sample period in Fig. 2. There is
meaningful variation in vacancy rates over space. They are generally higher in the less
prosperous north. Cities like Liverpool and Bradford, which respectively relied on
traditional port and port-related manufacturing or textiles, experienced decline from the
1950s. Apart from high unemployment and lower earnings there was outward migration tending
to generate a more obsolete housing stock and higher housing vacancy rates. Also in areas
where mining was historically important (in County Durham and Lancashire for example),
vacancy rates tend to be higher. We implicitly control for these geographical differences
in the industry composition by first differencing our empirical specification, thus
capturing all time-invariant characteristics that vary over space. The inclusion of the
first difference in the local unemployment rate as a further control should effectively
control for any relevant influence of changes in industrial structure on housing vacancy
rates. Refusal rates over the last 30 years have been clearly highest in the Greater
London Area and in the south of England and lowest in the north of the country (Fig. 3).
The south of England has not only been economically considerably more successful than
northern regions over the period, but it has (perhaps relatedly) had much tighter planning
restrictiveness. This – despite strong housing demand – has constrained the growth of
housing supply in southern England relative to the north.

<hs>  Econometric framework and identification</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

This specification only partly addresses the first endogeneity concern because there might
still be correlation with unobserved shocks. For example, in locations with increasing
demand, house prices and regulatory restrictiveness may increase simultaneously. Anecdotal
evidence suggests that in England regulatory restrictiveness is strongly pro-cyclical. In
times of high demand, planners reject more proposals in attractive areas, perhaps to avoid
what they perceive as a threatened ‘oversupply’ and perhaps because the system cannot cope
with the workload. Because housing supply takes time to adjust, this will lead to lower
local vacancy rates during boom periods. This again implies that α is likely strongly
downward biased if we estimate (2) by OLS. We therefore have to find an instrumental
variable to identify refusal rates that is uncorrelated with local unobserved shocks.
Bertrand and Kramarz (2002) exploit the cumulative representation of each political party
at regional level as an instrument for how restrictive French départments are likely to be
towards new retail entrants to document that stronger deterrence of entry by regional
zoning boards increased retailer concentration and slowed down employment concentration.
In a similar vein, Cheshire et al. (2015), Sadun (2015) and Hilber and Vermeulen (2016)
use the share of party representation at LA-level as an instrument to identify the impact
of local regulatory restrictiveness on, respectively, retail store-level output, the entry
of large retail stores, and house prices. Our study, to the best of our knowledge, is the
first to (i) exploit the fact that the particular details of the electoral system of local
government in England generates random variation in local party influence relative to vote
share and (ii) use this exogenous variation to identify the impact of local regulatory
restrictiveness on housing and Labour market outcomes. Our specific instrument is the
change in the number of seats for the Labour party between election years close to the
Census years. Traditionally Labour voters and politicians have been less opposed to new
residential construction than their Conservative counterparts. Labour councillors
typically represent a part of the population that has less housing equity and so is less
subject to NIMBY pressures aiming to protect house values. Labour councillors are also
likely to be more interested in the job generating effects of construction. Thus, we can
expect that an increase in the share of Labour seats may induce LAs to become less
restrictive, yet, a change in the share of Labour seats should not directly affect the
local vacancy rate other than through any effects it has on planning restrictiveness. To
make the reasons for our choice of instrument clearer it may help to have a brief
explanation of the English local government system and of the mechanics of the local
electoral system.13 There is a recent, succinct account available in Sandford (2016). The
English system is very heterogeneous but has certain common features. It is highly
centralised. As is discussed below, for most purposes, LAs are hardly more than agents of
central government with legal obligations but little fiscal autonomy; property taxes, for
example, are essentially national taxes (see Section 3.5) and there is no local income
tax. The major area of autonomy is with respect to planning decisions. There are a total
of 354 LAs of three different types: County Councils; District Councils; and Unitary
Authorities. The 125 Unitary Authorities – which have the fullest range of functions –
include the London and Metropolitan Boroughs. Members of the Councils of all LAs are
elected for ‘wards’ – geographical subdivisions of the council's area – and all elections
are conducted on a ‘first-past-the post’ system. Some LAs have single-member wards, others
multi-member wards. Voters vote for as many councillors as there are vacant seats at any
date there is an election. So if, for example, all members of a three-member ward face re-
election on the same date, the elector will have three votes. To complicate matters
further some councils elect all their members every three years; others elect one third of
their members at any given election while a few elect half their members each year, so
political control can change rapidly. Over the period of our analysis there were three
main political groups: The Labour, Conservative and Liberal-Democrat parties. As with any
first-past-the post system the party winning a seat contested by three parties may have a
minority of votes; in wards where one party is dominant, their candidate may have only
token opposition or even none at all. Equally, councils may be quite evenly split in terms
of vote shares for the different parties. Thus there are two independent reasons why the
share of votes at any election and the share of seats on the council may differ. The first
is just the way that the first-past-the-post voting system works when there are three
parties all gaining significant vote shares but those shares are highly variable between
constituencies. The second is that in many councils only one third or a half of the
elected members are voted for at any election. So the composition of the council is a
moving average of past votes. And, of course, the share cast for any party may change
significantly over the course of even a year. The result is that the share of votes and
the number of members on a council is not perfectly correlated—for the purposes of our
identification strategy important: the discrepancy between the two can be considered
random. The correlation between the share of Labour votes and seats, for example, is 0.77.
As is explained in Appendix 1, the variable we use for ‘seats’ is the closest measure we
can find for ‘seats controlled on the council’ so allows for the fact that in many
councils only a third or a half of members are elected in any given election. To
illustrate the random element of seats won beyond vote shares, in Fig. 4, we provide a
scatterplot of the share of Labour votes and share of Labour seats from 1978 to 2011 for
each year and LA. Not surprisingly there is a strong positive correlation between seats
and votes. However, below a vote share of about one third, any vote share translates into
a less than proportional number of seats (denoted by the dashed line). In a number of
cases, votes did not translate into any seats at all. Furthermore, because of the first-
past-the-post feature of the system, above a vote share of about one third, an increase in
the vote share leads to a more than proportional number of seats. If the Labour party has
a vote share of > 70%, this usually implies that all seats are assigned to the Labour
party. By including LA fixed effects ηℓ, we control for all linear trends caused by
unobservable factors, which increases the likelihood that changes in the instruments are
uncorrelated with Δϵℓ, t. Despite the fact that we identify changes in regulatory
restrictiveness from the random component generated by the particular features of the
English local government system, one might still be concerned that greater Labour
representation does not only affect regulatory restrictiveness but may also affect other
local variables that may separately affect local vacancy rates. That is, the exclusion
restriction may be violated. To address this crucial concern we first argue and provide
evidence to support the claim that — unlike in countries with decentralised government
structures — LAs in England, especially since 1972, have very little fiscal discretion or
power other than making planning decisions.14 Next, we show that even for those LAs —
Unitary Authorities — that provide more local services than others, the effect of a random
increase in the local Labour representation has a very similar effect on local
restrictiveness. This suggests that the relation between the share of Labour seats and
local restrictiveness may not be significantly biased by other local policies and services
that may be correlated with both regulatory restrictiveness and local vacancy rates. Most
reassuringly, when we run a battery of placebo (first-stage) specifications, in which we
replace the change in local refusal rates with changes in local expenditures — our placebo
variables — we find no significant relationship between share Labour seats and these
placebo measures (see Section 3.5). This is in contrast to a strong and statistically
significant negative relationship between the random change in the share of Labour seats
and local refusal rates. Overall, these results provide a strong indication that the
exclusion restriction is not violated and our identification strategy is valid.

<hs>  Results for housing vacancies</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We start by ignoring any potential endogeneity issues and simply regress the vacancy rate
on the refusal rate of major residential projects (Eq. (1)). From Fig. 5 we can see that
the cross-sectional relationship between the major refusal and the vacancy rates is
negative. The regression line implies that a one standard deviation increase in refusal
rates is associated with a 0.23 percentage point decrease in the vacancy rate (s.e.
0.040). This naïve correlation provides ‘common sense’ evidence supporting the view that
vacant houses can be ‘regulated away’. However, the quantitative impact is not very large.
Table 2 reports estimates for Eqs. (2) to (6). In the cases of Eqs. (3) to (6) these are
the second stage results of our IV-estimates. In column (1) we regress the change in the
vacancy rate on the change in the refusal rate still ignoring potential endogeneity issues
(Eq. 2). We first difference controls to offset for any time invariant omitted
characteristics such as differences in income levels across LAs. We see that even without
instrumenting for the refusal rate or adding control variables, the relationship between
(the change in) planning restrictiveness and (the change in) the vacancy rate is no longer
negative and statistically significant. However, because of the endogeneity concerns
discussed above, the coefficient on the refusal rate cannot be interpreted as a causal
effect. So in column (2) we include LA fixed effects. The coefficient on the change in the
refusal rate variable now becomes positive and statistically significant at the 10% level.
In column (3) of Table 2 we add further controls as discussed in Section 3.1 above. The
estimated coefficient for the change in the refusal rate is hardly affected, although it
is not statistically significant at conventional levels anymore. The control variables
often have a statistically significant impact on the change in the vacancy rate with the
anticipated sign. For example, areas with an increasing share of elderly people or of
council housing experience an increase in the vacancy rate. Also, areas with an increasing
unemployment rate, from which people may have been tending to move away, experience an
increase in the vacancy rate. In areas with a rising share of highly educated people,
vacancies tend to decrease. Still, however, regulatory restrictiveness is likely measured
with error (because developers may not apply in the first place in more restrictive
places). It may also be correlated with unobserved shocks. Moreover, we should address the
potential reverse causality issue that higher vacancy rates may induce policy makers to be
more restrictive. We therefore instrument for the change in the refusal rate with the
change in the share of Labour seats in column (4). This specification corresponds to Eq.
(3) above. Kleibergen-Paap F-statistics indicate that there are no issues of weak
identification of regulatory restrictiveness. The results suggest that a one standard
deviation increase in the refusal rate leads to an increase in the vacancy rate of 0.82
percentage points. As noted in the previous subsection, one objection to the instrument is
that it may be correlated with unobserved characteristics of the area. To control for
this, we include LA fixed effects in column (5) – corresponding to Eq. (4). The
coefficient on the refusal rate hardly changes and remains statistically significant at
the 5% level. Column (6), corresponding to Eq. (5), includes the same range of control
variables as in column (3). This makes almost no difference to the estimated coefficient
of primary interest. One might still be worried that changes in the share of Labour seats
are correlated with unobservable shocks (e.g. gentrification) that simultaneously have an
impact on voting behaviour and vacancy rates. So in column (7) we estimate our final model
(6). That is, we additionally include a flexible function of changes in the share of
Labour votes in local elections, approximated by a fifth-order polynomial to isolate the
impact of voting behaviour caused by any change in the demographic and socio-economic
composition of the LA from political power (measured by seats). In the sensitivity checks,
discussed below, we report results for different orders of polynomials. Reassuringly, the
estimated effect of regulatory restrictiveness in column (7) is very similar to the
previous specifications. The instrument is somewhat less strong (with a Kleibergen-Paap
F-statistic of 8.2). Still, we find a positive and economically meaningful effect of
regulatory restrictiveness on the vacancy rate: a one standard deviation increase in the
refusal rate increases the vacancy rate by 0.90 percentage points. Due to the correlation
between changes in the Labour vote shares and changes in the share of Labour seats, it is
no surprise that the coefficient is now only statistically significant at the 10% level.15
In Table 3 we report the corresponding first-stage estimates: a standard deviation
increase in the share of Labour seats leads to a decrease in the refusal rate of 0.26–0.34
standard deviations. It is notable that the first-stage coefficients of the change in the
share of Labour seats instrument are highly statistically significant and are hardly
affected by the inclusion of LA fixed effects and other control variables. If we include
vote share controls, the coefficient on change in Labour seats becomes slightly lower, but
it is still statistically significant at the 5% level.

<hs>  Results for commuting distance</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In Section 2 we hypothesised that a positive relationship between restrictions and vacancy
rates might be explained by increased mismatch. There are few obvious measures of mismatch
but for reasons discussed earlier we think that the ‘average commuting distance from the
workplace’ does not only provide a useful measure but can potentially illuminate in a
useful way the underlying interrelationship between spatial housing and Labour markets.
Moreover longer commutes unambiguously signal a welfare loss. One of the most important
characteristics of a house is its location with respect to jobs. It seems reasonable
therefore that the average commuting distance from the workplace should capture mismatch
in this dimension of housing characteristics for any given housing market. In principle,
households have a preference to live close to their workplaces. If regulatory restrictions
make it more difficult for people to find a home ‘matched’ to their preferences on other
characteristics close to work, their search takes longer and will extend further. This
adaptation of search behaviour implies, other things equal, vacancies will tend to be
higher in the more restrictive LAs and lower in neighbouring, less restrictive ones, as
workers become more locationally mismatched.16 We provide evidence that regulation also
has an impact on other proxies for mismatch in Section 3.6. Table 4 replicates Table 2
except that the log of average commuting distance replaces the vacancy rate as the
dependent variable. The results very closely parallel those for vacancies. Those in the
first column suggest that commuting distance is not influenced by regulatory
restrictiveness in the LA of the workplace. When we include LA fixed effects and
demographic control variables in columns (2) and (3), the results are still statistically
insignificant. This is not too surprising as the refusal rate is highly endogenous and
correlated with other factors that might explain commuting distances. For example, places
that have become denser might have tended to become more restrictive (Hilber and Robert-
Nicoud, 2013), but denser places also might have shorter commutes because jobs and
households are located closer to each other. In column (4) we therefore control for other
factors that might be correlated with the refusal rate by instrumenting for the change in
the refusal rate with the change in the share of Labour seats, as in Table 2. This reveals
a positive and significant effect. As restrictiveness in the LA in which a worker is
employed increases so does the average commuting distance: a one standard deviation
increase in the refusal rate in the workplace LA increases the commuting distance of its
employees by 8.5%, a non-negligible effect. The effect becomes somewhat smaller (5.8%)
when we include in column (5) LA fixed effects. The effect continues to be essentially the
same when we add further control variables in column (6) and a flexible function of the
share of Labour votes in column (7), with 5.9 and 6.1% respectively. In the last column
the effect is somewhat imprecisely estimated and only statistically significant at the 14%
level.17 On the other hand, the results are consistent in pointing towards a meaningful
effect of regulatory restrictiveness on commuting distance, and therefore increasing the
spatial mismatch between home and work locations.

<hs>  Evidence in support of the identification strategy</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The central assumption of our identification strategy is that a random increase in the
local representation of the Labour party only influences local regulatory restrictiveness
and does not separately affect other local decisions that may themselves be correlated
with local vacancy rates. If this assumption does not hold, then the exclusion restriction
is violated. In this context it is important to first re-emphasise that LAs in England
have considerable discretion over local planning decisions. However, unlike, for example,
in the US, they have almost no local fiscal resources and very limited ability to
determine local public service levels since these are largely set by central government.
To a large extent local jurisdictions – LAs – are simply agencies of central government in
charge of delivering services locally to regulated national criteria using a dedicated
budget stream for each purpose (such as education, social services, local roads and street
cleaning or refuse collection). These direct grants of revenue from central government
have over the past 75 years or so accounted for some 80% of LA spending. Revenues from
taxes on residential property are subject to revenue equalisation across LAs so that local
resources are ‘needs’ based and revenues to LAs become, with only a short delay,
independent of the local property tax base: commercial property taxes since 1990 have been
a national tax. Over the first half of the 20th Century LAs did gain an increasing role in
the provision of social housing – ‘council housing’. This was not initially designed to be
‘safety net’ housing for the very poor and deprived but rather public housing for those
not wanting or not able to become owner occupiers. At the start of the 20th Century owner
occupation as a tenure accounted for only about 10% of all housing. Council houses were
built to common nationally set design guidelines but delivery was under local control as
was the setting of rents (subject to the wider financial rules governing LAs' budgets).
This housing role of local government peaked in the 1950s and 1960s and declined
thereafter. By the late 1980s the construction of LA (council) housing had almost stopped
and local powers to set rents had been all but abolished. The two key changes were the
Housing Finance Act of 1972, which required LAs to set nationally defined ‘fair’ rents,
and the introduction of the Right to Buy for LA tenants, introduced in 1980.18 Tables 5
and 6 provide empirical evidence to support the above account of how limited the powers of
LAs in England are except for their powers over development. In Table 5 we test whether
the provision of public services is affected by the political composition of an LA more
directly by looking at expenditures on services, such as education, personal services
(e.g. social care), highways, (social) housing and planning. We then run a series of
placebo tests by replicating the preferred first-stage results in column (7) of Table 3,
but using different dependent variables. Instead of the change in the refusal rate we use
the log change in the following variables: education expenses, social services expenses,
highway expenses, local housing expenses, local planning expenses, and total local
expenses.19 Our identification strategy stipulates that a random change in the share of
Labour seats should only significantly reduce the refusal rate but should not affect the
expenditures on various public services. Indeed, that is what Table 5 reveals. The
coefficients for the change in the share of Labour seats on expenses are in all cases
highly statistically insignificant. The only exception is a weakly significant effect on
the total local expenditures (p-value = 0.15). The coefficient seems to suggest that a one
a standard deviation increase in the share of Labour seats increases local spending by
8.75%. Although the effect is not statistically particularly strong, one may be worried
that the share of Labour seats has a direct impact on vacancy rates via the total
expenditures of local planning authorities, which would call into question the exclusion
restriction. In Appendix 2 (Table A2.1) we therefore re-estimate the preferred
specification in Table 2 (column (7)), but include expenditure by category, one by one, as
additional controls (columns (1) to (5)). In column (6), Table A2.1, we instead include
total local expenditures as an additional control. The results show that the impact of the
refusal rate on vacancy rates is essentially unaffected, even when we control for total
local expenditures or for each category of expenditure individually. Planning expenses
seem to have some direct negative impact on vacancy rates (column (5)): more planning
expenses lead to lower vacancy rates. In column (6) we show that, even if the share of
Labour seats might have a positive effect on total local expenditures, it seems that local
expenditures do not have a direct impact on vacancy rates. Hence, this provides additional
evidence that the exclusion restriction holds. We repeat this exercise in Table A2.2,
Appendix 2 with commuting distance as dependent variable and show that the estimated
coefficients are also very similar to the baseline specification. Table 6 provides further
evidence supporting this narrative. First we replicate our baseline results but we allow
for the coefficient on the share Labour seats to vary between Unitary LAs and all other
LAs. Unitary Authorities have a wider remit in terms of the types of services they can
provide. We therefore use as an instrument the change in the share Labour seats interacted
with a dummy indicating whether an LA is not a Unitary Authority and control directly for
the change in share Labour seats interacted with a dummy indicating whether an LA is a
Unitary Authority. The first-stage results, reported in Panel A of Table 6, reveal that
the coefficient on the share Labour seats is similar for the two types of LAs: the
coefficient for Unitary Authorities is somewhat lower but not statistically significantly
different from the coefficient for other LAs. This also suggests that the local share of
Labour seats does not significantly affect the nature and quality of local service
provision (which in turn might be correlated with regulatory restrictiveness and local
vacancy rates). Indeed, Panel B of Table 6 shows that the baseline results for vacancy
rates are essentially unaffected. Finally if we replace the vacancy rate by the log
commuting distance in Panel C of Table 6, the results are again similar. This is
indicative that LAs with a greater remit of service provision are not fundamentally
different from those that have a more limited remit—presumably this is because even
Unitary Authorities have very little discretion over services other than planning
decisions.

<hs>  Other evidence for the importance of mismatch</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As noted in Section 2 we also investigate the impact of local restrictiveness on other
symptoms or measures potentially capturing mismatch, such as the rate of new construction,
the share of properties which are crowded, the share of non-permanent properties and
migrants. The results are shown in Table 7. We replicate the preferred specification where
we instrument for the refusal rate and include fixed effects and control variables (as in
column (7) in Tables 2 and 4).20 We first investigate a symptom of restrictiveness which
would be expected to induce greater mismatch: whether in more restrictive areas, despite
the effect on prices, it is more difficult to build additional houses. Because the refusal
rate should have an impact on the absolute number of dwellings, we regress the change of
the number of dwellings (rather than logs) in an LA on the refusal rate, while
additionally controlling for the number of dwellings (in levels).21 Column (1) of Table 7
shows that on average over a ten year period, a one standard deviation increase in
regulatory restrictiveness in an LA reduces the number of additional dwellings by more
than half a standard deviation of the growth in the number of dwellings over this time
period (about 1800 dwellings per LA). To make sure that this effect is not entirely
explained by larger LAs we include a fifth-order polynomial of the number of dwellings and
control for house prices in column (2). In line with expectations, a higher price is
associated with a slower growth in the number of dwellings, most likely because higher
prices are predominantly found in already developed areas with fewer possibilities to
extend the building stock (see Hilber and Vermeulen, 2016). More relevantly for present
purposes, the effect of regulation on new dwelling supply is essentially unaffected once
we control for prices. Another symptom of mismatch is the share of officially classified
‘crowded’ properties – properties with more than one person per room: some 2% of all
properties. If households cannot find a property to their liking and cannot afford larger
properties, they are likely to end up in smaller properties, perhaps staying with their
partner in the parental home. Column (3) in Table 7 shows that there is indeed a positive
effect of regulation on the share of crowded properties. One may argue that this results
from the fact that tighter controls make housing more expensive so that households will
occupy smaller homes with fewer rooms. However, when we control for house prices in column
(4) the effect of regulation on the share of crowded properties is very similar, even
somewhat stronger. House prices are, as expected, positively associated with crowding. The
coefficient indicates that a standard deviation increase in the refusal rate leads to a
0.58 percentage points increase in the share of crowded properties (about one-third of a
standard deviation). Hence, although the results are only significant at the 10% level,
the implied magnitude of the point estimates is non-negligible. A further symptom or proxy
for mismatch is explored in columns (5) and (6) of Table 7, the share of non-permanent
dwellings. Our underlying explanation for why this measure should proxy for housing market
mismatch is that in more restrictive markets there is an incentive to accept even less
optimally matched housing characteristics in the short term in order to intensify and
increase the efficiency of search. Living in temporary accommodation – mainly caravans or
trailers - has a low switching cost associated with it and is a cheaper strategy than
buying a suboptimal place to live and then reselling it when a more suitable house is
found. The ease with which search can be undertaken and its effectiveness will increase if
the house-hunter can be physically present in the local market (Ha and Hilber, 2013).
Moreover since the chances of finding a better match in the housing market will improve
with length of time spent searching then there will be a payoff to having temporary
accommodation available for searchers in markets where matching is more difficult. Thus in
more restrictive LAs, other things equal, matching is more difficult and the share of
temporary dwellings is greater. Although by improving the efficiency of search, temporary
housing may itself reduce vacancies of permanent dwellings, it is such a relatively sub-
optimal form of housing we would expect house-hunters to resort to it only when there is
extreme difficulty in matching their preferences to available housing supply. So we would
expect that the net share of temporary housing would be positively correlated with local
restrictiveness. In column (5), Table 7, we find weak but consistent evidence that more
restrictive markets have a higher rate of non-permanent homes. Given that the change in
non-permanent homes is a somewhat noisy and indirect proxy for mismatch, it may not be too
surprising that the results are not statistically significant at conventional levels.22
Column (6) addresses the issue that this may be entirely the result of higher house
prices. This does not seem to be the case; indeed the effect becomes somewhat stronger.
The coefficient implies that a standard deviation increase in the refusal rate leads to an
increase in the share of non-permanent homes of 0.213 percentage points (about one-third
of a standard deviation). This positive relationship is certainly consistent with the
proposition that more restrictive local planning increases the costs of matching would-be
house buyers in the local housing market to the available permanent housing, inducing
people to live temporarily in caravans and mobile homes – clearly inferior substitutes to
houses. In column (7) of Table 7 we show the results for yet another symptom or proxy for
mismatch. We expect that tighter regulation in an LA makes it harder for people to move
into the preferred area and find a new, satisfactory property in it. Hence, we expect that
the share of in-migrants, defined as households that had a different address in the
previous year, is lower. We initially find only very weak evidence supporting this
proposition with a p-value of 0.15. But migration responds not just to spatial differences
in wages but also to house price differences across space. So in column (8) we control for
house prices. Although house prices are indeed negatively correlated with the share of
migrants, controlling for house prices increases the effect of regulation. Not only is the
relevant coefficient larger but it is now significant at the 10% level. The coefficient
implies that a standard deviation increase in the refusal rate leads to a reduction in the
share of migrants of 1.53 percentage points (almost half of a standard deviation), a
substantial effect in economic terms.

<hs>  Other potential explanations</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Are there other explanations for the positive relationship between restrictions and
vacancy rates? One might, for example, expect tighter policy restricting the elasticity of
supply to be associated with greater price volatility and for that to be associated with
higher vacancy rates. This is because price volatility might create a (real) ‘option to
wait’ (McDonald and Siegel, 1986; Grenadier, 1995, 1996). The greater the uncertainty
(price volatility) the more valuable is a property owner's option to delay selling or
renting out the property. Especially in markets with lengthy leases – such as office
markets – this can generate high and persistent (“sticky”) vacancy rates; landlords are
better off keeping their units empty. We would expect the real options argument to be less
important in the British residential property markets compared to office markets, however,
since demand volatility tends to be lower (people have to live somewhere) and, for
rentals, the length of tenancy agreements is typically quite short (a year or even less).
The real options argument, nevertheless, could be relevant since tight regulation (more
inelastic supply) amplifies demand shocks, so we would expect price volatility to respond
more strongly to demand volatility in places with tighter regulatory constraints. We proxy
house price volatility by calculating the coefficient of variation of house prices in the
year of observation and the three years that follow. Demand volatility is proxied by the
coefficient of variation of earnings based on the year of observation and the three years
that follow. The results (reported in Panel A of Table 8) show that at least according to
the instrumental variable specifications (columns (4) to (7)), the sensitivity of price
volatility with respect to earnings volatility increases with regulatory restrictiveness.
This provides some evidence that regulatory constraints potentially could increase vacancy
rates by increasing price volatility (i.e. increased price volatility raises the value of
the real option to keep properties empty), but when we investigate this possibility
further (see results in Appendix 2, Table A2.3 and discussion below) the evidence does not
appear to support it. In Appendix 2 we estimate regressions where we directly control for
commuting distance from the workplace, price volatility and room diversity. In Table A2.3
we show that the coefficient on the (instrumented) refusal rate variable decreases by
about 15% and ceases to be statistically significant at conventional levels once we
control for commuting time (column (1)). This suggests that at least a part of the
positive effect of a change in regulatory restrictiveness on the change in vacancy rates
is driven by mismatch in the housing market, as proxied by commuting time. When we instead
control for price volatility (column (2)), interestingly, the effect of the refusal rate
on vacancy rates increases somewhat in magnitude and is statistically significant. This
finding could be interpreted as suggesting that the real options argument does not play an
important role in explaining the positive link between regulatory restrictiveness and
vacancy rates. When we include room diversity in column (3) the effect of regulation on
vacancy rates again becomes somewhat stronger, although it is close to that estimated in
the baseline specification. Room diversity is, as expected, positively correlated with
vacancy rates; when diversity is one standard deviation higher, vacancy rates are 0.65
percentage points higher. We finally control for all variables, including the change in
the share of crowded properties, the share of non-permanent properties and the share of
in-migrants (column (4)). The coefficient related to the refusal rate is very similar to
the previous specifications. We should note two caveats. First, our proxies, for mismatch
in particular, are at best partial and, in the case particularly of the share of crowded
and temporary properties, as well as the share of in-migrants, more symptoms than
measures, so we would not expect these variables to fully account for the positive impact
of the (change in the) refusal rate on the (change in the) vacancy rate. Second, the
findings reported in Table A2.3 should generally be interpreted with caution. This is
because both the commuting distance and the price volatility are likely highly endogenous,
as are the alternative proxies for mismatch (some of them have the opposite sign from what
might have been expected). Hence, the reported coefficients are likely biased. Still,
overall, we interpret the results reported in Table A2.3 as indicating that the increased
mismatch between the preferences of the local residents and the characteristics of the
available local housing stock causally contributes to our key finding of a positive impact
of tighter local restrictiveness on local vacancy rates. This finding is certainly
plausible in the context of the extraordinarily rigid British planning system. Whether
similar effects can be observed in other countries is an interesting question.

<hs>  Sensitivity analysis</hs>
  ~~~~~~~~~~~~~~~~~~~~

Finally, we conducted a set of robustness checks. We tested 1) the sensitivity of our
choice of polynomial in relation to changes in the share of Labour votes; 2) the possible
endogeneity of earnings; 3) whether results are driven by idiosyncratic factors associated
with the Greater London Area; 4) whether the results are sensitive to including all
refusals of residential development, not just refusals of applications for major
developments; 5) whether a fixed effects approach rather than first differencing makes any
difference to the main findings; and 6) whether the change of the Census definition of
vacancies in 2011 affects our findings. The main results survive all these tests and
alternative specifications essentially unchanged. The results are set out in detail in
Appendix 2.

<h>CONCLUSIONS</h>
-----------

This is the first attempt to rigorously analyse the impact of land use regulation on the
spatial and temporal variation in housing vacancy rates. It would come as no surprise to
economists to observe that in well-functioning Labour markets there was unemployment.
Workers search for jobs and employers seek (better) qualified workers. Attempting to
regulate unemployment away makes no sense. Vacant houses are equivalent to unemployed
workers yet, at least in Britain, policy does try to ‘regulate’ vacant homes away by using
their existence to justify being more restrictive in the control of the supply of new
homes and the structural adaptation of existing ones. In this paper we argue that such
restrictions have two main opposing effects on housing vacancies. The ‘opportunity cost
effect’ leads to a lower vacancy rate in the more restrictive housing markets because
supply constraints lead to higher prices, and thus to higher opportunity costs of keeping
housing vacant. The ‘mismatch effect’, however, implies higher vacancy rates in the more
restrictive housing markets because households will find it more difficult to match their
preferences to the characteristics of the local housing supply given their budget
constraints. So search becomes more prolonged and costly and households choose to search
for properties further afield and commute longer. We do indeed confirm that there is a
simple negative correlation between local planning restrictiveness and local housing
vacancies. Superficially this appears to support the planners' ‘common sense’ that the
existence of empty houses means they can – even should – plan to be more restrictive in
supply. This unconditional correlation, however, is the result of a form of joint
causation. When we effectively control for unobserved characteristics at the local level
by using first differencing, the negative correlation turns positive. When we further
control for local linear trends, for other potential explanatory variables and account for
the endogeneity of local regulatory restrictiveness, the causal effect of restrictiveness
on vacancy rates is firmly positive, statistically significant and economically
substantial. Our empirical analysis does not fully unpack the box of explanations. It is a
reduced form telling us what the net impact of increased planning restrictiveness is on
housing vacancies. If an LA becomes more restrictive, signalled by an increase in the rate
of refusal of residential development proposals, then all else equal, vacancy rates
increase in that LA. We also provide direct evidence that mismatch may be an important
reason for higher vacancy rates in more restrictive housing markets: The more restrictive
in planning terms a local jurisdiction is, the longer is the average commuting distance of
workers within it. We subject these findings to an extensive range of sensitivity
analyses. They survive remarkably unaltered. Welfare implications in markets with search
frictions are not easy to derive. This is because in such a second best world, households
may search less or more than would be welfare optimal (Koster and Van Ommeren, 2017). This
paper does not set out to assess the net welfare impact of tightening the supply of
housing. However, because regulatory constraints seem to worsen matching for households,
the effect of tighter restrictions on vacancies and commute times unequivocally generates
a welfare cost. It is the mismatch between the preferences of households and the housing
stock on offer that leads, other things equal, to higher vacancy rates in the more
regulated – typically more desirable – places. This is not to say that tighter regulatory
constraints in some places necessarily increase vacancy rates at the aggregate level (for
the whole country). However, even if on aggregate vacancy rates were unaffected by
regulatory restrictiveness, such constraints will still likely cause a significant welfare
loss. This is because too much housing stays empty in the most regulated, most desirable
and, by implication, most productive places with the strongest demand and highest
valuations for living space. So people are induced to commute further, while living in the
“wrong” places. There are important implications for policy, particularly for the UK
because of its extraordinarily restrictive planning system. Crucially planners should not
allocate less land for development on the grounds that there are empty houses. Some
vacancies are integral to the well-functioning of any market and, as our results show,
trying to ‘regulate housing vacancies away’ is counterproductive. There is moreover a nice
irony for advocates of the ‘compact city’. The most common policy to attempt to implement
this ideal is to impose growth boundaries (make land scarcer) and be more restrictive to
adaptations of the existing stock or – in the US – make it more difficult to obtain zoning
ordinance waivers. In summary aiming for a compact city makes planning policy more
restrictive. Our results show this will have exactly the opposite to the intended effect
because average commuting distances will lengthen as residents search further afield for
housing they can afford and matches their preferences.


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<ART>Exchange rate uncertainty and international portfolio flows: A multivariate GARCH-in-mean approach
================================================================================

Authors: Guglielmo Maria Caporale, Faek Menla Ali, Nicola Spagnolo
DOI: 10.1016/j.jimonfin.2015.02.020
Year: 2015  |  Pages: 70-92
ASJC codes: 2002, 2003
Keywords: Bond flows, Causality-in-variance, Equity flows, Exchange rate uncertainty

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper examines the impact of exchange rate uncertainty on different components of net portfolio flows, namely net equity and net bond flows, as well as their dynamic linkages. Specifically, a bivariate VAR GARCH-BEKK-in-mean model is estimated using bilateral monthly data for the US vis-à-vis Australia, Canada, the euro area, Japan, Sweden, and the UK over the period 1988:01-2011:12. The results indicate that the effect of exchange rate uncertainty on net equity flows is negative in the euro area, the UK and Sweden, and positive in Australia. The impact on net bond flows is also negative in all countries except Canada, where it is positive. Under the assumption of risk aversion, the findings suggest that exchange rate uncertainty induces a home bias and causes investors to reduce their financial activities to maximise returns and minimise exposure to uncertainty, this effect being stronger in the UK, the euro area and Sweden compared to Canada, Australia and Japan. Overall, the results indicate that exchange rate or credit controls on these flows can be used as a policy tool in countries with strong uncertainty effects to pursue economic and financial stability.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The macroeconomic effects of exchange rate uncertainty, especially on trade flows, have
received considerable attention since the collapse of the Bretton Woods system in 1971 and
the adoption of floating exchange rates in March 1973, both in the theoretical and
empirical literature (see McKenzie, 1999, for a comprehensive review). By contrast, such
effects on financing activities, in particular on equity and bond portfolio flows, have
not been thoroughly examined. In addition, there is a substantial literature examining the
determinants of international asset transactions, but there are very few empirical papers
analysing the impact of exchange rate uncertainty. For example, Bohn and Tesar (1996)
found that investors tend to move to markets where returns are expected to be high. The
validity of this ‘return chasing’ hypothesis has been confirmed by Bekaert et al. (2002),
who found that positive return shocks lead to an increase in short-term equity capital
flows using data from 20 emerging countries. Portes et al. (2001) and Portes and Rey
(2005), by contrast, showed that financial transactions are explained by the gravity model
at least as well as goods trade. More recently, Fratzscher (2012) found evidence that push
factors were important drivers of net capital flows during the recent financial crisis,
but not during the recovery period (2009–2010), when domestic pull factors were dominant,
especially for emerging countries in Asia and Latin America. The underlying idea is that
exchange rate volatility increases the costs of international financial transactions and
reduces potential gains from international diversification by making the acquisition of
foreign securities such as bonds and equities more risky, which in turn affects negatively
portfolio flows across borders. Indeed, Eun and Resnick (1988) had previously shown that
exchange rate risk is non-diversifiable and has an adverse impact on the performance of
international portfolios. This finding is also consistent with the evidence presented in
the study by Levich et al. (1999), who found, by surveying 298 US institutional investors,
that foreign exchange risk hedging constitutes only 8% of total foreign equity investment.
Further, Choi and Rajan (1997) reported that foreign exchange risk has a significant
effect on asset returns in seven major developed countries other than the US, and that
ignoring such a factor results in misspecification when analysing the integration or
segmentation of international capital markets. By considering a wide range of developed
and emerging market economies, Fidora et al. (2007) and Borensztein and Loungani (2011)
also found that exchange rate volatility is an essential factor for bilateral equity and
bond portfolio home bias. Eun and Resnick (1988) suggested that hedging through forward
exchange contracts and multicurrency diversification are effective ways to reduce exchange
rate risk. Glen and Jorion (1993) and Eun and Resnick (1994) provided further evidence
that hedging in the forward exchange markets improves the performance of diversified
portfolios of equities and bonds. Jorion (1991) also found that the exchange rate risk is
diversifiable. In particular, his empirical findings provided little evidence that US
investors require compensation for bearing the exchange rate risk. Gehrig (1993), instead,
argued that exchange rate risk, purchasing power risk, and capital market restrictions are
insufficient factors for explaining equity portfolio home bias, whilst informational
segmentation plays a key role. Finally, Hau and Rey (2006) provided a theoretical
framework for analysing the implications of incomplete foreign exchange risk trading for
the correlation structure of exchange rate changes and equity returns, as well as exchange
rate changes and net portfolio flows1; however, they did not carry out any statistical
tests for the impact of exchange rate uncertainty on portfolio flows across borders. The
present paper makes a fourfold contribution to the existing literature. First, it analyses
empirically whether exchange rate uncertainty affects international portfolio flows and
their variability using a bivariate VAR GARCH (1, 1)-in-mean framework. It is in fact the
first empirical investigation of this kind, based on bilateral monthly data for the US
vis-à-vis six developed economies, namely Australia, Canada, the euro area, Japan, Sweden,
and the UK over the period 1988:01-2011:12. The analysis is based on longer monthly time
series and differs from previous studies which focus on the determinants of home bias and
international financial transactions using panel and cross-sectional techniques (see, for
examples, Portes and Rey, 2005; Fidora et al., 2007; Bekaert and Wang, 2009; Batten and
Vo, 2010; Borensztein and Loungani, 2011; Mishra, 2011; Mercado, 2013; Daly and Vo, 2013).
We use the most common time series measure of uncertainty found in the literature, i.e.
the conditional variance modelled as a GARCH (1, 1) process2 (others are the continuous
volatility measure in Portes and Rey (2005), the stochastic deviation from purchasing
power parity (PPP) in Fidora et al. (2007) and Mishra (2011), the standard deviation of
exchange rate changes in Bekaert and Wang (2009) and the coefficient of variation of the
real exchange rate in Mercado (2013)). This approach is flexible enough to allow for joint
estimation of the relationship between uncertainty and portfolio flows taking into account
past information on perceived uncertainty.3 Second, unlike Hau and Rey (2006), who assumed
that the supply of bonds is infinitely elastic, thereby simplifying the dynamics of bond
acquisitions in their model, we examine the impact of exchange rate uncertainty on the
individual components of portfolio flows across borders, i.e. on net bond and equity flows
(as well as their variability) in turn. According to Hau and Rey (2006), exchange rate
uncertainty should affect equity, but not bond flows. Fidora et al. (2007) and Borensztein
and Loungani (2011), by contrast, found evidence that bond flows exhibit stronger home
bias compared to equity flows. We provide some relevant empirical evidence on this issue.
Third, existing empirical studies on the relationship between exchange rate changes and
portfolio flows investigate short-run dynamic interactions only with linear dependence
techniques (i.e., first moment analysis). For example, Brooks et al. (2004) and Hau and
Rey (2006) use simple correlations and regression analysis for the US vis-à-vis the euro
area and Japan, and 17 OECD countries, respectively; Siourounis (2004), Chaban (2009), and
Kodongo and Ojah (2012) estimate VAR models respectively for four developed countries (the
UK, Japan, Germany, and Switzerland), three commodity-exporting countries (Canada,
Australia, and New Zealand), and four African countries (Egypt, Morocco, Nigeria, and
South Africa) vis-à-vis the US. Their results are characterised by significant deviations
from normality and conditional heteroscedasticity, i.e., volatility clustering or so-
called ARCH effects (see Engle, 1982) that are not captured by their setup. By contrast,
we model the first and second moments simultaneously to analyse the dynamic interactions
between exchange rate changes and portfolio flows. In this way, we capture the volatility
in the flows and exchange rate changes which is well documented in the economics and
finance literature, and address some of the potential pitfalls of earlier studies. Fourth,
since volatility is a measure of the information flow (see Ross, 1989), it is of paramount
importance to understand how the stochastic information arrivals in the form of simple
portfolio investment shifts in bonds and equities are transmitted to the foreign exchange
market, and vice versa. Furthermore, knowledge of the response of investors to exchange
rate uncertainty provides important information to policy-makers and regulators to
formulate appropriate policies based on imposing or relaxing credit controls on these
flows depending on the state of the economy, with the aim of achieving economic and
financial stability. For example, if exchange rate uncertainty dampens net inflows,
expansionary policies to boost the economy during recessionary periods could be
unsuccessful if exchange rates are too volatile. In such circumstances, credit controls on
inflows may be relaxed, and such a policy is likely to increase inflows, thereby boosting
the economy. In addition, financial and economic stability can be pursued by reducing
exchange rate volatility. The remainder of the paper is organised as follows. Section 2
describes the data and carries out some preliminary analysis. Section 3 outlines the
econometric model and the hypotheses tested. Section 4 discusses the empirical results,
and finally Section 5 concludes.

<h>DATA DESCRIPTION AND PRELIMINARY ANALYSIS</h>
-----------------------------------------

We examine the impact of exchange rate uncertainty on different components of net
portfolio flows, namely net equity and net bond flows, as well as their dynamic linkages
for the US vis-à-vis Australia, Canada, the euro area, Japan, Sweden, and the UK.
Throughout, the US is considered the domestic or home economy. The data on portfolio
investment flows, obtained from the US Treasury International Capital (TIC) System,4 are
monthly and cover the period from 1988:01 to 2011:12 for all series. The reason for
selecting this start date is that cross-border portfolio flows for the period preceding
1988 are known to be negligible (see Brooks et al., 2004). Net equity (bond) flows are
calculated as equity (bond) inflows minus outflows. While inflows are measured as net
purchases and sales of domestic (US) assets (equities and bonds) by foreign residents,
outflows are the net purchases and sales of foreign assets (equities and bonds) by
domestic residents (US). In the case of the euro area, we aggregate the data for the
individual EMU countries (Austria, Belgium–Luxembourg,5 Finland, France, Germany, Ireland,
Italy, the Netherlands, Portugal, and Spain) to extract cross-border bond and equity flows
between the US and this region. Positive numbers imply net equity and bond inflows (in
millions of US dollars) towards the US or outflows from its counterparties. Moreover,
since without scaling model convergence is difficult to achieve, we use monthly averages
to adjust these flows, specifically the average of their absolute values over the previous
12 months as in Brennan and Cao (1997), Hau and Rey (2006), and Chaban (2009) among
others. Following more recent papers in the literature (e.g., Chaban, 2009; Kodongo and
Ojah, 2012), the exchange rates are end-of-period data, defined as US dollars per unit of
foreign currency6; the source is the IMF's International Financial Statistics (IFS).
Exchange rate changes are calculated as Et = 100 × (PE,t/PE,t−1) where PE,t stands for the
log of the exchange rate at time t. For the period preceding the introduction of the euro,
i.e. before 1999, we use US dollar per ECU as the euro area's exchange rate. Descriptive
statistics are displayed in Table 1. The mean of monthly exchange rate changes is positive
(a US dollar depreciation) for Japan and Canada, and negative (a US dollar appreciation)
for the rest of the countries. On the other hand, the monthly mean of net equity flows is
positive for Sweden and Canada and negative for the remaining countries, indicating equity
inflows from Sweden and Canada towards the US and outflows from the US towards the other
countries. The monthly mean of net bond flows is negative for Australia and positive for
the other countries. This indicates the existence of bond inflows from all countries
except Australia (for which there is evidence of bond outflows) vis-à-vis the US. Exchange
rate changes are found to exhibit higher volatility than the two types of flows.
Furthermore, equity flows appear to be characterised by higher volatility than bond flows
(although their volume is very small). As for the third and fourth moments, exchange rate
changes, net equity flows, and net bond flows all exhibit skewness and excess kurtosis in
most cases. The Jarque–Bera (JB) test statistics imply a rejection at the 1% level of the
null hypothesis that exchange rate changes and the two types of flows are normally
distributed in all countries in question. Table 2 reports the LM ARCH test statistics for
the residuals of the fitted bivariate VAR model εi,t, where i = 1 corresponds to exchange
rate changes, and i = 2 to net flows (equity and bond flows in turn, since the analysis is
bivariate). At the 10% significance level, the results indicate the presence of ARCH
effects up to order 6 in all variables, except for net equity flows for Australia and net
bond flows for the euro area.

<h>EMPIRICAL RESULTS</h>
-----------------

The objective of our analysis is to establish whether exchange rate uncertainty affects
net equity and bond flows across borders, and also whether there is volatility
transmission (hence information flows) between these flows and exchange rate changes and,
if so, in what direction causality runs.11 The QML estimates of the bivariate VAR GARCH
(1, 1)–BEKK-in-mean parameters as well as the associated multivariate Q-statistics
(Hosking, 1981) are displayed in Tables A1–A6 (see Appendix A) for Australia, Canada, the
euro area, Japan, Sweden, and the UK, respectively.12 Panels A and B in each Table concern
the bivariate regression of exchange rate changes against equity and bond flows
respectively. The Hosking multivariate Q-statistics for (6) and (12) lag orders for the
standardised residuals in the exchange rate changes-equity flows cases indicate no serial
correlation at the 5% level, when the corresponding conditional mean equations are
specified with p = 1 for Japan, p = 2 for Sweden and p = 3 for the other countries (the
insignificant parameters in the mean equations have been dropped13). With regard to the
exchange rate changes-bond flows relationships, whilst no dynamic terms appear to be
necessary for Sweden, setting p = 1 for the UK, p = 2 for the euro area, p = 3 for
Australia and Canada and p = 5 for Japan is required to capture adequately the dynamic
structure in these cases. Also, the Hosking multivariate Q-statistics for (6) and (12) lag
orders for the squared standardised residuals suggest that the multivariate GARCH (1, 1)
structure is sufficient to capture the volatility in the series. Hence, the estimated
models are shown to be well specified. Table 3 reports a summary of the estimated results
displayed in Tables A1–A6 (Appendix A). These suggest that there are limited dynamic
linkages between the first moments compared to the second ones. The results in the
conditional mean equations indicate the existence of bidirectional mean spillovers between
exchange rate changes and net bond flows in Japan, as well as spillovers from net bond
flows to exchange rate changes in Canada and the UK, and from net equity flows to exchange
rate changes in the euro area. The results also suggest that exchange rate uncertainty
affects net equity flows negatively in the euro area, Sweden, and the UK, and positively
in Australia, and has no effect in Canada and Japan. Its impact on net bond flows, on the
other hand, appears to be negative in all countries except Canada for which it is
positive. In Fig. 1 we plot net equity and net bond flows, exchange rate changes, and the
conditional variances of exchange rate changes for all countries over the sample period.
It can be seen that the conditional variances of exchange rate changes, measured using the
bivariate VAR GARCH-in-mean parameterisation, were high during the recent global financial
crisis in most countries.14 The impact of the 1992 crisis is also apparent in the cases of
the UK and the euro area. Interestingly, net inflows towards the US were low during the
recent crisis period in most cases, and also during the 1992 crisis, especially for the
UK. Overall, these plots support the econometric results implying that periods of high
exchange rate uncertainty were associated with declines in net flows. This holds in most
cases, except Australia and Japan for net equity flows and Canada for both net equity and
net bond flows. The estimated negative impact of exchange rate uncertainty on net equity
as well as net bond flows has important implications. First, it indicates that risk-averse
market participants, especially those of the counterparties to the US, respond to exchange
rate uncertainty by reducing their financial activities, and favouring domestic rather
than foreign securities in their portfolios to minimise their exposure to uncertainty.
This finding is broadly consistent with the evidence in Bayoumi (1990), Iwamoto and van
Wincoop (2000), and Bacchetta and van Wincoop (1998, 2000). While Bayoumi (1990) showed
that net capital flows as a share of GDP are lower during the floating exchange rate
period (1965–1986) than during the gold standard (1880–1913), Iwamoto and van Wincoop
(2000) reported that net capital flows as a fraction of GDP are much larger across regions
of a country, which use the same currency, than across countries. Bacchetta and van
Wincoop (1998, 2000), on the other hand, showed that exchange rate uncertainty should
dampen net international capital flows in the context of a two-period general equilibrium
model. Second, in contrast to Hau and Rey (2006), who assumed that bonds are hedged
instruments not affected by exchange rate uncertainty, it appears that uncertainty in fact
affects bond as well as equity flows, and the former more widely, since a negative impact
is found in five of the six countries examined (see also Fig. 1). This is consistent with
the results of Fidora et al. (2007), who found that exchange rate volatility is an
important factor for bilateral portfolio home bias, this being higher for bonds than for
equities. This finding has recently been confirmed by Bekaert and Wang (2009) and
Borensztein and Loungani (2011), although in the former study it is not found to be
economically significant. The rationalisation of Fidora et al. (2007) of the higher home
bias for bonds compared to equities is that it is consistent with Markowitz-type
international CAPM specifications in which less volatile financial assets should be
characterised by a larger home bias. However, the results indicate that exchange rate
uncertainty does not induce home bias in Australia and Japan for equity flows and in
Canada for both equity and bond flows (see also Fig. 1). The finding that exchange rate
uncertainty has a positive effect on net equity flows in Australia is consistent with the
evidence in Batten and Vo (2010) and Daly and Vo (2013), whilst Mishra (2011) found a
negative effect. A possible explanation for the findings of Australia and Canada may be
that they are commodity-exporting countries and developments in their financial markets
are driven by terms-of-trade shocks. Chaban (2009) and Ferreira Filipe (2012) indeed found
that the portfolio-rebalancing motive of Hau and Rey (2006) in these countries is weak.
Chaban (2009) argued that commodity prices play a significant role in the transmission of
shocks in these countries, and Ferreira Filipe (2012) found that differences in the
volatility of country-specific shocks also do so. Japan is a special case: as highlighted
by Hau and Rey (2006), bond flows represent most of the international portfolio flows for
this country, even though a high percentage of Japanese debt is financed internally. The
estimates of the conditional variance equations indicate that the conditional variances
exhibit persistence in all cases except for net equity flows in Canada (see Tables A1–A6
in Appendix A). While the persistence of the conditional variance of exchange rate changes
ranges from 0.54 (Japan) to 0.98 (euro area), that of the corresponding flows ranges from
0.38 (Sweden) to 0.91 (euro area) for net equity flows and from 0.43 (Japan) to 0.98
(Canada) for net bond flows. The ARCH, a11, and GARCH, b11, parameter estimates for
exchange rate changes in the bivariate GARCH–BEKK models are rather similar, regardless of
whether the relationship with net bond or equity flows is considered (see Panels A and B
respectively in all Tables). More specifically, a11 changes by a magnitude of less than
0.10 and this also applies to b11, except for Japan where it is around 0.26. Furthermore,
the off-diagonal elements of the ARCH and GARCH matrices suggest the following:
statistically significant volatility spillovers running from net equity flows to exchange
rate changes (measured by b21) in the cases of Canada and the UK; both shock (measured by
a21) and volatility (measured by b21) spillovers from net equity flows to exchange rate
changes in the case of Sweden, and bidirectional volatility spillovers (measured by b21
and b12) for Japan. The results also show that net bond flows' shocks affect the
volatility of exchange rate changes (a21) in the case of Australia; shock and volatility
spillovers running from exchange rate changes to net bond flows are present for Canada,
whereas for Sweden they run in the opposite direction; in the case of Japan there are
volatility spillovers from exchange rate changes to net bond flows. In the euro area and
the UK the volatility spillovers between net bond flows and exchange rate changes are
bidirectional. Finally, exchange rates' shocks are found to affect the volatility of net
bond flows in the UK, whereas in the euro area shock spillovers run in the opposite
direction. Broadly speaking, these findings are consistent with those of the causality-in-
variance (i.e., the information flow) test results (Table 3). More specifically, the Wald
test statistics (see Tables A1–A6) provide evidence of strong causality-in-variance from
net equity flows to exchange rate changes in the case of the UK and Sweden, and
bidirectional causality-in-variance in the case of Japan. There is also causality-in-
variance from net bond flows to exchange rate changes in Australia and Sweden, and
causality in the reverse direction in Canada, as well as bidirectional causality in the
rest of the countries. A possible explanation for the existence of stronger dynamic
linkages between exchange rate changes and bond flows instead of equity flows is that
foreign exchange dealers usually follow bond yields in their trading behaviour; these
yields, in turn, drive cross-border bond acquisitions, which results in volatile exchange
rates. Spillovers from the exchange rates may be due to the fact that investors adjust
their portfolios on the basis of their volatility. Finally, Fig. 2 displays the evolution
of the dynamic conditional correlation between exchange rate changes and net flows to
provide further insights into the dependence between these variables. The graphical
analysis indicates that these correlations are time-varying in most cases. Furthermore,
there are clear shifts during turbulent periods such as the 1992 crisis in the case of the
UK, and the recent global financial crisis of 2007–2009 in most cases. These plots confirm
the existence of strong linkages between exchange rate changes and net flows during such
periods, as found before.

<h>CONCLUSIONS</h>
-----------

In this paper, we have analysed the impact of exchange rate uncertainty on net bond and
net equity flows, as well as the dynamic linkages between exchange rate volatility and the
variability of these flows, using monthly data for the US vis-à-vis six advanced
economies, namely Australia, Canada, the euro area, Japan, Sweden, and the UK over the
period 1988:01-2011:12. By estimating bivariate VAR GARCH-BEKK-in-mean models, we find
evidence that exchange rate uncertainty impacts on net equity flows negatively in the euro
area, Sweden, and the UK and positively in Australia. Furthermore, in contrast to the
assumption of Hau and Rey (2006), it also affects net bond flows negatively in all
countries except Canada, where the effect is positive. The general conclusion that can be
drawn from these results is that exchange rate uncertainty induces risk-averse investors,
especially those of the counterparties to the US, to reduce their financial activities and
to favour domestic rather than foreign assets in their portfolios in order to minimise
their exposure to uncertainty. This evidence is stronger in the case of the UK, the euro
area and Sweden compared to Canada, Australia and Japan. The results for Australia, Canada
and Japan may be due to the specific characteristics of these economies, as documented in
other studies (e.g., Hau and Rey, 2006; Chaban, 2009; Ferreira Filipe, 2012). The
causality-in-variance analysis suggests the existence of strong spillovers from net equity
flows to exchange rate changes in the UK and Sweden, and bidirectional causality-in-
variance in Japan. Causality-in-variance is also found to run from net bond flows to
exchange rate changes in Australia and Sweden, in the opposite direction in Canada, and in
both directions in the other countries. Overall, our findings have important policy
implications that are country-specific. In particular, they suggest that policy-makers and
economic and financial regulators in countries with strong uncertainty effects can use
exchange rate or credit controls on equity as well as bond flows as instruments to achieve
economic and financial stability.


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<ART>Exploring mortgage interest deduction reforms: An equilibrium sorting model with endogenous tenure choice
================================================================================

Authors: Amy Binner, Brett Day
DOI: 10.1016/j.jpubeco.2014.12.005
Year: 2015  |  Pages: 40-54
ASJC codes: 2002, 2003
Keywords: Endogenous public goods, Equilibrium sorting models, Mortgage interest deduction, Tenure choice

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<h>ABSTRACT</h>
--------

In most equilibrium sorting models (ESMs) of residential choice across neighborhoods, the question of whether households rent or buy their home is either ignored or else tenure status is treated as exogenous. Of course, tenure status is not exogenous and households' tenure choices may have important public policy implications, particularly since higher levels of homeownership have been shown to correlate strongly with various indicators of improved neighborhood quality. Indeed, numerous policies including that of mortgage interest deduction (MID) have been implemented with the express purpose of promoting homeownership. This paper presents an ESM with simultaneous rental and purchase markets in which tenure choice is endogenized and neighborhood quality is partly determined by neighborhood composition. The public policy relevance of the model is shown through a calibration exercise for Boston, Massachusetts, which explores the impacts of various reforms to the MID policy. The simulations confirm some of the arguments made about reforming MID but also demonstrate how the complex patterns of behavioral change induced by policy reform can lead to unanticipated effects. The results suggest that it may be possible to reform MID while maintaining the prevailing rates of homeownership and reducing the federal budget deficit.

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<h>INTRODUCTION</h>
------------

The promotion of homeownership has been a widespread and long-term focus of public policy
(Andrews and Sanchez, 2011). Support for such policies derives both from political
ideology and from a belief that homeownership delivers positive spillovers. Homeowners, it
is argued, have greater incentives to invest in the physical and social capital of their
communities, thus providing private and public benefits. There is a substantial body of
empirical evidence that lends credence to this view. Homeownership is strongly correlated
with property condition and maintenance (Galster, 1983), neighborhood stability (Dietz and
Haurin, 2003; Rohe and Stewart, 1996), child attainment (Bramley and Karley, 2007; Green
and White, 1997; Haurin et al., 2002), citizenship (DiPasquale and Kahn, 1999) and lower
crime rates (Glaeser and Sacerdote, 1996; Sampson and Raudenbush, 1997).1 A wide variety
of policy measures have been implemented to promote homeownership. Attempts have been made
to encourage the supply of mortgage lending; for example, in the U.S. through the
establishment of Government Sponsored Entities providing liquidity and security for
mortgage lenders. Policies have also been implemented to encourage particular groups into
homeownership; for example, in the U.K. through the Right to Buy scheme for social housing
tenants and more recently the Help to Buy schemes for equity loans, mortgage guarantees
and new buyers (NewBuy). Homeownership has also been promoted through the tax system e.g.
through exemptions from capital gains tax on property sales and mortgage interest
deduction (MID). MID, the focus of this paper, allows taxpayers to subtract interest paid
on a residential mortgage from their taxable income. MID is present in the tax laws of
many countries including the U.S., Belgium, Ireland, the Netherlands, Switzerland and
Sweden and was previously offered in the U.K. and Canada. It was introduced in the U.S. in
1913 when the homeownership rate was 45.9%. Under MID and numerous other initiatives,
homeownership rose after the Second World War reaching a peak of 69% in 20042. Currently,
MID constitutes the second largest US tax expenditure3 with the cost estimated to be some
$104.5 billion dollars in foregone tax revenue in 2011 (Office of Management and Budget,
2011). In the context of a large US fiscal deficit, MID has come under increased scrutiny.
It has been argued that rather than encouraging homeownership the tax subsidy is simply
capitalized into property values making properties no more and potentially less affordable
than without the policy (Glaeser and Shapiro, 2002; Hilber and Turner, 2010). Furthermore,
critics contend that MID most greatly benefits high-income taxpayers who would likely be
homeowners irrespective of the tax incentives (Shapiro and Glaeser, 2003). Certainly
higher income households are more likely to own their homes, hold larger mortgages and
itemize mortgage interest payments on their tax returns (Poterba and Sinai, 2008). Of
course, courtesy of their higher incomes, they also itemize at a higher rate (Glaeser and
Shapiro, 2002). As a result, in 2004 the government paid an average $5459 in MIDs to
households earning over $250,000 compared to $91 for households earning below $40,000
(Poterba and Sinai, 2008). In the face of strong opposition, particularly on the part of
financial services interests and housing lobbyists, repeated efforts to reform MID in the
U.S. have borne little fruit Ventry (2010)4. Over the last three budget cycles the U.S.
administration proposed reforms to MID, but on each occasion those initiatives have failed
to pass into law. The key element of those proposals was to limit MID for households
paying the top marginal rates of income tax. Other proposals for reform include; replacing
MID with a system of tax credits (Dreier, 1997; Follain et al., 1993; Green and Vandell,
1999), scrapping MID in order to fund cuts in federal income taxes (Stansel, 2011) and
replacing MID with a fiscal incentive open only to first time buyers (Gale et al., 2007).
The debate is fueled by a lack of clarity with regard to how such reforms will play out.
Clearly, eliminating the MID will increase the cost of borrowing for the purposes of
buying property and, ceteris paribus, cause demand for owned properties to fall. This
reasoning underpins the National Association of Realtors claim that “eliminating the MID
will lower the homeownership rate in the U.S.”5. Of course, it is recognized that the
impact of eliminating the MID also depends on supply conditions in the property market.
The extent to which falling demand translates into reductions in homeownership as opposed
to falling prices depends on the price elasticity of housing supply. Bourassa and Yin
(2008) estimate that for some groups the negative effect of losing MID may be more than
outweighed by the positive effect of falling property prices; homeownership amongst such
groups could actually rise as a result of eliminating the MID. What is less widely
recognized is that changing market conditions in the property market will have
ramifications in the closely associated rental market. Falling demand for homeownership
can translate into rising demand for rental housing. More complex still is the interplay
between homeownership and the desirability of residential locations. Since residential
location choice is endogenous to the problem, eliminating MID may not only encourage the
movement of individuals between ownership and rental but also the migration of households
between neighborhoods. While numerous attempts have been made to identify the impacts of
eliminating the MID (e.g. Bourassa and Yin, 2008; Hilber and Turner, 2010; Toder, 2010)
those studies have been based on a partial characterization of the problem. This paper
develops a model that more completely describes the complex adjustments in spatially
defined and interrelated property markets and uses that model to explore some of the
possible ramifications of MID reform. The model developed in this paper is an equilibrium
sorting model (ESM) (Kuminoff et al., 2010). ESMs provide a framework within which it is
possible to examine how households choose their residential location from a set of
discrete neighborhoods. As reviewed in Section 2, ESMs have been developed to examine a
number of economic issues relating to choice of residential location. As far as we are
aware, however, our model is the first ESM to simultaneously model purchase and rental
markets while endogenizing tenure choice. In Section 3 the innovations of the model are
outlined in detail; particularly the specification of a neighborhood level of public good
provision whose value depends, in part, on endogenous levels of homeownership and the
development of an adjustment process to policy reform that accommodates capital gains. To
elucidate the pathways of adjustment that MID reform may initiate in property markets,
Section 4 presents a simple two-jurisdiction calibration of the model based on the 2000
census data for Boston, Massachusetts. The calibrated model is used to simulate four
different MID reform proposals; capping MID at a rate of 28%, replacing MID with
refundable tax credits, scrapping MID and reducing income taxes and replacing MID with a
lump sum payment to new owners. The simulations allow us to examine several important
questions with regard to MID reform. In particular, to explore how reforms may impact
property prices, levels of homeownership, the distribution of welfare across income groups
and the mixing of income groups within and across jurisdictions. Our analysis suggests
that, contrary to existing claims, with the right policy design it may be possible to
reform MID while maintaining the prevailing rates of homeownership, increasing public
goods provision and contributing to a reduction in the federal deficit.

<h>EQUILIBRIUM SORTING MODELS</h>
--------------------------

In essence, equilibrium sorting models (ESMs) provide a stylized representation of the
interactions of households, landlords and government within a property market. Originally
developed to explain observed patterns of socio-economic stratification and segmentation
in urban areas (e.g. Ellickson, 1971; Epple and Romer, 1991; Oates, 1969; Schelling, 1969;
Tiebout, 1956), ESMs provide a formal account of the process whereby heterogeneous
households sort themselves across the set of neighborhoods within a property market.
Neighborhoods, it is assumed, differ in quality according to the level of public goods
each provides. Those public goods may reflect purely physical attributes of a location
(for example, a neighborhood's proximity to commercial centers) or the levels of provision
of local amenities (for example, the quality of local schools). An important
distinguishing feature of ESMs is in allowing local amenity provision to be shaped by
endogenous peer effects; that is to say, by the characteristics of the set of households
that choose to locate in a neighborhood. Epple and Platt (1998), for example, present a
model in which local taxes and lump sum payments are determined by the voting preferences
of the residents in a neighborhood; these computationally complex models often have no
closed form solution and are instead solved using numerical computation. Similarly,
Ferreyra (2007) and Nesheim (2002), present models in which school quality is related to
measures of the average income of households in a locality. In an ESM, the mapping of
households to quality-differentiated neighborhoods is mediated through property prices.
Indeed, a solution to an ESM is taken to be a set of property prices that support a Nash
equilibrium allocation of households to neighborhoods such that the supply and demand for
properties are equated in all neighborhoods. While some simple ESMs have closed form
solutions equilibria for more complex models, particularly those including endogenous
neighborhood quality, are usually calculated using techniques of numerical simulation
(Bayer et al., 2004; Ferreyra, 2007). Over the last decade ESMs have increased in
popularity and complexity. Recent modeling extensions allow for moving costs (Bayer et
al., 2009; Ferreira, 2010; Kuminoff, 2009), overlapping generations (Epple et al., 2010)
and simultaneous decisions in a parallel labor market (Kuminoff, 2010). In addition, the
ESM framework has been used to explore empirical data on the distribution of households
and property prices in order to derive estimates of the value air pollution (Smith et al.,
2004), school quality (Bayer et al., 2004; Fernandez and Rogerson, 1998) and the provision
of open space (Walsh, 2007). ESMs have also been used to explore policy issues such as
school voucher schemes (Ferreyra, 2007), open space conservation (Klaiber and Phaneuf,
2010; Klaiber, 2009; Walsh, 2007) and hazardous waste site clean ups (Smith and Klaiber,
2009). A comprehensive review can be found in Kuminoff et al. (2010). One area that has
received relatively little attention in the ESM literature is that of tenure. Indeed, the
vast majority of ESM applications make the assumption that households rent their
properties from absentee landlords. Where different tenure statuses have been considered,
those applications have treated tenure status as a fixed characteristic rather than a
choice variable (Bayer et al., 2004; Epple and Platt, 1998). In reality, of course,
households choose from a number of tenure options, with the key distinction being between
ownership and renting. The joint decision of tenure and housing consumption has been
examined in the real estate literature. For example, King (1980) estimated preferences for
the UK housing market developing an econometric model of joint tenure and housing demand.
Similarly, Henderson and Ioannides (1986) consider joint housing decisions in the US and
Elder and Zumpano (1991) developed a simultaneous equations model of housing and tenure
demand. For a number of issues, such as the reform of MID policy, the choice of tenure is
the central consideration of the policy debate. Accordingly, one of the key contributions
of this paper is to describe an ESM in which tenure choice is endogenized. In our model,
household choices whether to rent or purchase property are a function of market
conditions, including the endogenous provision of local public goods. When policy reforms
result in price changes in the property market, homeowners and renters are affected
differently. In particular, homeowners will be impacted by capital gains (or losses) that
are not experienced by renters. The modeling framework developed in the next section
outlines a method for incorporating such distinctions.

<hs>  The economy</hs>
  ~~~~~~~~~~~

Consider a closed spatial economy consisting of a continuum of households. The model is
closed insomuch as households may not migrate in or out of the economy. Households differ
in their incomes, y. They also differ in terms of their preferences over the amount of
housing they consume, β, and the value they attach to owning a property, θ. Ownership
preferences represent the private returns to homeownership that are not realized when
renting. Such private returns are motivated by numerous considerations including i)
freedom to modify housing, ii) satisfaction from homeownership status and iii) anticipated
financial returns from capital gains. The distribution of household types in the
population is defined by the joint multivariate density function f(y, β, θ). The economy
is divided into a set of spatially discrete neighborhoods, j = 1, …, J. In our model, each
neighborhood is assumed to have its own local government. As such, we refer to these areas
as jurisdictions. Each jurisdiction is characterized by a vector of local public goods, gj
= {zj,1 …, zj,U, qj,1, …, qj,V}, comprising U exogenous elements, zj,u, and V endogenous
elements, qj,v. The level of provision of endogenous elements is determined by the
composition of the set of households that choose to reside within a jurisdiction. The
provision of public goods is assumed to be homogenous within a jurisdiction.

<hs>  The demand side</hs>
  ~~~~~~~~~~~~~~~

To reside in jurisdiction j household i must buy housing there. The decision to rent, R,
or own, O, housing is referred to as tenure choice. We describe the set of tenure options
as T = {R, O} Accordingly, our model is characterized by households choosing to
participate in one of a number of property markets each defined by a jurisdiction and
tenure bundle, {j, t}. Households also choose a quantity of housing; a decision
approximating real life choices over the size and quality of home to buy or rent.6 Housing
is defined as a homogenous good that can be owned or rented from absentee landlords at a
constant per unit cost, pj, within a jurisdiction7 (Epple and Romer, 1991; Epple and Sieg,
1998; Epple and Platt, 1998; Bayer et al., 2004; Ferreyra, 2007). The quantity of housing
demanded by a household in market {j, t} is denoted hj,t = h(p, g, τp; y, β, θ, m, δ). The
two arguments in that function yet to be explained (m and δ) concern the borrowing a
household must assume in order to purchase a property. In particular, to become a
homeowner a household must take out a mortgage8 and pay mortgage interest, m, to the
lender. Mortgage interest is paid only on the amount borrowed, where that borrowing is
determined by the value of the housing purchased, pjhj,t multiplied by a loan-to-value
ratio, δi. Differences in δi can be interpreted as representing the varying abilities of
households to make a down payment. Property taxes τp are paid on both rented and purchased
housing. Accordingly, the implicit subsidy a household, i, receives by itemizing mortgage
interest and property tax payments on their tax return, MID(p, h, τp, y, m, δ), is
endogenous to the household's decision and depends upon the purchase price of property
(not including tax), p, the quantity of housing demanded, h, the property tax rate, τp,
and household income, y (which in our model also determines the loan-to-value ratio, δ,
and the probability that a household itemizes).

<hs>  Local public goods</hs>
  ~~~~~~~~~~~~~~~~~~

Notice that our specification assumes that public good provision is increasing in the
homeownership rate: a relationship that might imply homeownership has a direct effect on
local public good provision or that homeownership simply proxies for unobserved inputs
that themselves have a direct effect. The presence of xj in the public good production
function defines a peer effect whereby community characteristics, perhaps median household
income, affect the provision of public goods. Such peer effects have considerable
empirical support (Nechyba, 2003) and have been incorporated in a number of existing ESM
specifications (Nesheim, 2002; Ferreyra, 2007).

<hs>  The household optimization problem</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Households derive utility from local public goods, g, consumption of housing, h, and other
consumption, c. Preferences for local public goods are determined by parameter α, which is
assumed to be constant across households. Meanwhile, housing quantity preferences are
determined by parameter β, which is assumed to vary across households. Our model also
allows for the fact that households can derive more utility from housing when they own
their home than when they rent it (or vice versa). Each household is characterized by
values for the preference parameter set θ, which scales the utility derived from housing
in the utility function for home owning. Finally, households select the jurisdiction and
tenure combination that maximizes their level of utility.

<hs>  Simulating responses to exogenous policy change</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In reality policy changes occur in a world in which households already rent or own
existing properties. That reality influences the outcome of a policy change in at least
two ways. First, changes take place in the context of an existing housing stock whose
quantity and location has been determined by households' initial choices. Second, a
household's current tenure status determines whether their choices following the policy
change are influenced by capital gains.10 To see that more clearly, it is instructive to
briefly contemplate how market changes impact differently on renters and owners. Consider
a change that leads to increased house prices. When prices go up existing renters are
unable to afford their current consumption bundle. Households can respond in a number of
different ways. They can alter their tenure choice, they can move to another location
where property prices are lower or they can reduce their demand for housing and
consumption. Indeed, they could do any combination of these. In contrast, owning a
property prevents rises in prices from making the current consumption bundle unaffordable;
homeowners are shielded against price increases. Instead, a rise in prices presents
homeowners with the opportunity to sell-up and use the capital gains to increase
consumption or relocate to a jurisdiction that provides more desirable public goods. To
simulate the process of adjustment in the property market within the context of what is
essentially a static model requires some careful consideration. We first assume that the
market is in a state of long-term equilibrium, an equilibrium achieved under the baseline
policy. Households have optimally chosen where to live, whether to rent or own and how
much housing to consume. To reflect that state of the world, we imagine a property market
in which all the housing units demanded under that baseline policy have been constructed
and that these existing housing units cannot be demolished in the face of a policy change
(though they can be repackaged and new units may be constructed). The policy change is
introduced to this world at a point after homeowners have paid for their current
properties at the pre-change prices but before rent has changed hands, consumption goods
have been bought and taxes and mortgage interest have been paid. As a result of the policy
change, households reconsider their choices of housing quantity, location and tenure
status and the model is solved for the set of property prices that bring the market back
to equilibrium under the changed conditions. For, households that were previously renting,
things are relatively simple: they either buy or rent at the prices determined by the new
equilibrium. In contrast, having bought at the prices characterizing the old equilibrium,
households that previously owned must make their new housing decisions in light of the
fact that the new price conditions may present them with capital gains or losses.

<h>SIMULATING MID REFORMS</h>
----------------------

The model developed above provides a rich environment in which to explore the general
equilibrium consequences of reforming MID policy. Within that environment the impact on
government expenditure, patterns of community composition, homeownership rates and the
levels and distribution of household welfare can be considered simultaneously. To
undertake this exercise it is preferable to examine a model that replicates the real
world. Such a model requires reasonable but tractable functional forms that can be
calibrated to produce a model resembling a real world property market. Following the
convention of Epple and Platt (1998) we specifically model Boston, using updated data for
2000. To provide a clear and accessible illustration of the pathways of change that
operate in light of a policy reform it is prudent to consider a simple two-jurisdiction
version of the model. While it is eminently possible to investigate problems with many
more jurisdictions, this simplification enables us to most clearly characterize the chain
of reactions that occur within property markets in response to policies that reform MID.
The model is coded in Matlab11 and uses simulation and iterative numerical techniques to
solve for market clearing prices and provision of endogenous public goods (Lagarias et
al., 1998)12.

<hs>  The proposed policy reforms</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~

The current debate regarding reform of MID policy is motivated in part by the large U.S.
deficit. Indeed, as part of plans to reduce that deficit, President Obama submitted
federal budget proposals in 2011, 2012 and 2013 that advised capping itemized deductions,
including MID, at 28%. Each time Congress has rejected the recommended tax reforms. All
the same, we take the proposal of capping MID at 28% as our first potential policy reform.
To be clear, under the current tax system homeowners are permitted to deduct mortgage
interest and property tax payments from their taxable income when calculating their income
tax bill. Those in the top three income tax brackets, therefore, are entitled to an
implicit rebate on those expenditures at their marginal tax rates of 31%, 36% and 39.6%
respectively. The cap limits that implicit rebate to 28%. Three alternative MID-reform
policies are also considered: a refundable flat-rate tax credit; an income tax reduction;
and a New Owner Scheme. To compare the various proposed policies, we make the assumption
that the central motivation for reform to the MID is reduction of the budget deficit.
Accordingly, we calculate the reduction in deficit brought about by our baseline reform of
a 28% cap on MID. The three alternative MID-reform policies are tailored to ensure that
they facilitate the same reduction in the budget deficit as the cap.13 Let us briefly
review the alternative MID-reform policies. First, replacing MID with a refundable14 flat-
rate tax credit has been advocated by both the Center for American Progress, who propose a
15% refundable tax credit, and the National Commission on Fiscal Responsibility (Moment of
Truth, 2010), who propose a 12% non-refundable mortgage interest tax credit. For the
purposes of our simulations, we model this reform as being a policy change in which MID is
abandoned and, instead, all households who are owners can claim back a flat-rate
percentage of their mortgage interest and property tax costs. As explained previously, the
flat-rate we apply in our subsequent simulations is chosen such that federal budget
savings achieved by this policy are identical to capping MID at 28%. Our second
alternative MID-reform policy follows the proposal made by the Reason Foundation (Stansel,
2011) to scrap MID and instead introduce a revenue neutral reduction in federal income tax
for all households. Here, we consider a policy in which MID is abandoned and a portion of
the savings in government expenditure are used to fund an equal percentage reduction in
income tax for all households. Again, to ensure comparability across our policy
simulations the level of income tax reduction is chosen such that the policy achieves the
same reduction in the federal government budget deficit as the other proposed reforms. Our
final alternative MID reform policy takes motivation from the First Time Buyers scheme
proposal made by Gale & Gruber (2007), which suggests scrapping MID and introducing a
refundable payment to first-time buyers in the first year after a property is purchased.
In the model this is achieved through a New Owner Scheme, which makes an equal lump sum
payment to new homeowners. Again in our simulations the level of payments to these first
time buyers is chosen so as to ensure comparability in the reduction of the federal budget
deficit across reforms.

<hs>  Calibration</hs>
  ~~~~~~~~~~~

To conduct the simulations, specific functional forms are selected for the structural
equations of the model. Following Epple and Platt (1998), parameter values for the
functions were calibrated such that our model approximates the reality of the Boston
Metropolitan (PSMA) area; though in our application we take data for Boston from 2000 and
not 1980. Table 1 presents a summary of important statistics for Boston in 2000 and Table
2 summarizes the parameters obtained by calibrating the model to that reality. The
assumptions and methods used in deriving those parameters are explained in the following
sections.

     <hss>Jurisdictions</hss>

        To allow the pathways of response to MID reform to be studied with reasonable
        clarity, we explore a simple two-jurisdiction version of the model. Extensions to
        multiple-jurisdiction models are relatively easy to implement, but greatly reduce
        the tractability of interpretation. Again following Epple and Platt (1998), we
        begin by dividing the Boston Metropolitan area into two jurisdictions, labeled A
        and B. Jurisdiction A provides a higher level of exogenous local public goods
        provision, consequently attracting a larger share of the population. Competition
        for access to public goods increases the price of housing in A relative to B,
        which leads to some income segregation. As a result the median household income in
        jurisdiction A is higher than that of B.

     <hss>Households</hss>

        Households in the model are characterized by three parameters; income, y, housing
        preference, β, and ownership preferences, θ. The first step in calibrating this
        model, therefore, is to establish the joint distribution of those parameters
        amongst the residents of Boston in 2000. As made explicit shortly, a Cobb–Douglas
        utility function is assumed such that a household's housing preference, βi, is
        related to the proportion of their income that they spend on housing. That data
        along with information on household income, yi, is available from the census which
        provides a cross-tabulation of the share of income spent on rent (and equivalently
        on monthly owner costs for owner–occupiers) by income. Accordingly, to establish
        the joint distribution of y and β we use maximum likelihood estimation to fit a
        bivariate-normal distribution flny, β) ∼ N(μf, Σf) to 2000 census data for
        Boston.15 Parameter values from that estimation are recorded in the first row of
        Table 2. Notice that β is negatively correlated with y, such that while high-
        income households spend absolutely more on housing than low-income households,
        that expenditure constitutes a smaller proportion of their income. For simplicity,
        and due to a lack of existing empirical evidence, it is assumed that household
        ownership preferences, θ, are independent of income and housing preferences.
        Accordingly, values were drawn from a lognormal distribution ln(θ) ∼ N(μθ, σθ2)
        with mean and variance chosen such that the baseline model predicts homeownership
        rates comparable to those observed in Boston in 2000.16 The parameters selected
        through that procedure are also recorded in Table 2. For the purposes of
        simulating our model, we create a sample of 2000 households with income, y, and
        preference parameters, β and θ, drawn from the calibrated distributions.17

     <hss>Taxes</hss>

        The property tax rate, τp, was set at the average level for Boston in 2000 using
        data supplied by the Massachusetts State Government. To capture the correlation
        between income and itemization rates, the probability of a household itemizing was
        calibrated using data on itemization rates by income from Poterba and Sinai (2008)
        which is reproduced in Table 2.18 In this calibration we model property taxes as
        if they are fully passed on to renters. This is aligned with a simplified
        interpretation of the economy in which housing is constructed and supplied at
        marginal cost including property taxes. In this situation, a competitive market
        would lead to the full incidence of the tax being levied upon renters. This
        assumption could be relaxed through further refinement of the property market
        model and the development of a buy-to-let market to expressly model differences in
        the tax burdens of owner–occupiers, landlords and renters.19

     <hss>Housing supply</hss>

        The assumption of a single housing supply function covering rental and purchase
        properties is motivated by considering the direct sale or rent of housing from a
        zero-profit housing constructor. If property is supplied in a single market,
        constructors must be indifferent between renting and selling properties. If they
        sell a property at marginal cost, they are no longer responsible for maintenance,
        depreciation and foregone interest. If the property is rented the constructor must
        include these costs in the rental price in order to break even. As a result, if
        housing for rent and purchase is produced for sale in a single market, both
        renters and purchasers must face the same per unit user cost of housing, although
        technically rents exceed purchase prices since homeowners pay the remaining user
        costs (e.g. maintenance costs) directly rather than to the constructor.21

     <hss>Local public goods</hss>

        For simplicity, the calibrated model considers one exogenously determined local
        public good and one endogenously determined local public good. The extension to
        multiple local public goods is trivial, but adds complexity to the interpretation
        of the simulation results. We use air quality to act as a representative exogenous
        local public good. In our simulation, air quality is defined in units of
        concentration of nitrogen oxides (measured in pphm) below the highest level
        observed in Boston in the Massachusetts Air Quality Report. Using that measure,
        the mean level for air quality in Boston in 2000 was 3. Accordingly we set air
        quality in jurisdiction B to that level but assume that jurisdiction A offers a
        slightly higher level of provision: 4. To test the sensitivity of our simulated
        equilibria to the assumption that homeownership directly impacts on local school
        quality, we explore two versions of the model. In the first version, a direct
        affect is assumed away. Rather homeownership is taken to proxy for a set of
        omitted factors that impact directly on school quality through channels that are
        independent of property market decisions. Since those omitted factors are taken to
        be unchanging, we progress by exogenously fixing the homeownership argument in the
        school quality production function at the observed Boston state average. In our
        simulations, the argument maintains that initial level despite adjustments in
        rates of homeownership that result from changes in MID policy. In the second
        version of the model the assumption of a direct affect is maintained. In our
        simulations, the homeownership argument in the school production function updates
        in response to changes in property market decisions brought about by reforms of
        MID policy. The results reported in Section 4 are derived from the first model
        version, assuming local homeownership has no direct impact on school quality
        (although local endogeneity is still present through expenditure per pupil and
        median incomes). Comparable results from the second model version, with an
        endogenous homeownership feedback, are presented in Section 5.2. Additional
        results exploring the sensitivity of the results to sample size, the strength of
        preferences for public goods and alternative housing supply specifications are
        available from the authors upon request. As a general comment, the patterns of
        relocation suggested by the model are the same for both versions under each
        reform. It is notable, however, that when local homeownership rates are assumed to
        directly affect the provision of local public goods the magnitude of welfare gains
        associated with reforms that increase homeownership rates are sensitive to this
        assumption.

<hs>  Results</hs>
  ~~~~~~~

The long-run equilibrium under current policy conditions was calculated for our simulated
sample of 2000 households.25 The impact of MID-reform was then investigated using an
iterative solution algorithm to calculate the new equilibrium characterizing the property
market when each of our four proposed policy reforms was instituted from that baseline.
Tables 4 and 5 describe important features of the equilibrium in the baseline and for each
policy-reform scenario. Table 4 presents a characterization of those equilibria in terms
of the composition and characteristics of the households in each jurisdiction. Table 5
characterizes the equilibria from the perspective of households in each of the six tax
brackets. Throughout our discussion of the results we will use the term “price” to refer
to the price inclusive of property tax since this is the effective price faced by
households.

     <hss>Baseline with MID</hss>

        Consider the results displayed in the first rows of Tables 4 and 5 that describe
        the equilibrium that evolves under the current system of MID. In the baseline,
        jurisdictions A and B differ initially only in their exogenous provision of public
        goods (Column 1 of Table 4). The higher exogenous public good provision in
        jurisdiction A shapes the resulting equilibrium. Households prefer a greater
        provision of public goods which increases demand for housing in A relative to B.
        Consequently, the population of A is higher than the population of B, with 65% of
        all households residing there (Column 2 of Table 4). As the supply of housing in A
        is not infinitely elastic, relatively stronger demand in A drives the prices of
        housing in A above the prices in B. The purchase price of housing (including
        property tax) is $7379 in A compared to $5496 in B (Column 3 of Table 4). Price
        differences between jurisdictions and tenure options precipitate the
        stratification of households. Column 4 of Table 4 confirms that households with
        relatively strong ownership preference, θ1, choose to purchase housing while those
        with relatively weak ownership preference rent housing. Similarly, as can be seen
        from column 5 of Table 4, households that spend a relatively large proportion of
        their income on housing, e.g. those with relatively high β, prefer lower housing
        prices and tend to choose to reside in jurisdiction B. Since β is negatively
        correlated with income, this reinforces segregation by income. As shown in Columns
        1 and 2 of Table 5, only 19% of households in the lowest income tax bracket (1st)
        choose to live in A compared to 96% in the highest tax bracket (6th).
        Consequently, the median income of households in A is almost 3 times that of B
        (Column 7 of Table 4). Within each jurisdiction some households rent while others
        own. Recall from the calibration that households with higher incomes face
        relatively lower loan-to-value ratios and, under the existing MID policy, can
        itemize their mortgage interest and property tax costs at a relatively higher
        marginal rate. Accordingly, the marginal cost of purchasing housing is lower for
        higher-income households and, ceteris paribus, households with high incomes are
        more likely to become homeowners. As shown in Columns 7 of Table 5, only 52% of
        households with incomes below the standard deduction choose to own compared to 74%
        of households in the highest income tax bracket. This result is consistent with
        observed homeownership rates in Boston in 2000. Returning to Table 4, the
        concentration of higher income households in A leads the homeownership rate to be
        higher than in B (Column 8). Recall from Eq. (5) that local property tax revenues
        depend on both purchase prices and the total quantity of housing demanded in a
        jurisdiction. In the baseline equilibrium, higher property prices in A are
        slightly offset by larger property sizes in B such that tax revenue per household
        in A is marginally lower than in B; $22,266 and $22,344 respectively (Column 10 of
        Table 4). Larger local tax revenues translate directly into higher levels of local
        government expenditure on the endogenous public good. However, since median income
        is higher in A than B, jurisdiction A benefits from relatively larger provision of
        the public good through a stronger peer effect (Column 11 of Table 4). Overall,
        provision of the endogenous public good is higher in A, with a school quality
        score of 498, than it is in B, at 379. Combined with the exogenous public good
        provision this indicates that the index of public goods provision is 32% higher in
        jurisdiction A. That difference in provision of the public good acts to further
        exaggerate the patterns of sorting initiated by the initial difference in public
        goods provision.

        28% cap

        Now let us consider how things change when MID is capped at a rate of 28%. Under
        the new policy those households in the top three tax brackets who had previously
        been able to itemize their expenditures on mortgage interest and property tax at
        31, 36 and 39.6% respectively, would now be limited to itemizing at 28%. In the
        absence of other adjustments, the cap raises the per-unit cost of housing for the
        86% of households in the top three income tax brackets that itemize MID on their
        tax returns in the baseline. Characteristics of the new equilibrium are presented
        in the second row of results in Tables 4 and 5. The equilibrium outcome is the
        product of a number of forces: the immediate impact of the reform is to reduce
        demand amongst existing homeowners with a relatively strong housing preference.
        This reduction threatens to lower local expenditure on public goods through a
        reduction in property tax revenues, which precipitates the relocation of some
        renters from jurisdiction A to B, increasing housing demand in B and pushing up
        property prices there. In turn, this redistribution of the population leads to
        higher median incomes in both A and B (column 7, Table 4), and increases local
        expenditure on public goods in both jurisdictions. Those affects combine in
        precipitating a rise in the endogenous public good (proxied here by school
        quality) of 1% in A (to a score of 499) and 0.3% in B (to a score of 380). The
        slightly larger increase in public good provision in A makes it more desirable
        relative to B, this stimulates a rise in prices in order to avoid relocation of
        households from B to A and maintain the balance of supply and demand. Overall,
        property prices rise by roughly 1.04% in A and 1.23% in B despite the removal of
        MID. Comparing results in column 9 of Table 4 we can see that mean rental property
        sizes fall; this is a consequence of the relocation of households with relatively
        small housing consumption from A to B and the rise in prices26. However, as
        anticipated we also see a contraction in mean housing consumption across tax
        brackets four to six (see Table 5), however homeownership rates in A and B are
        left almost entirely unchanged (identical to 2 s.f.). It is worth taking a moment
        here to reflect on the adjustment in prices. Intuitively, one might assume that
        the cap on MID increases the marginal cost of housing for individuals in the top
        tax brackets, which in turn leads to a contraction in their demand. It follows
        that from this partial equilibrium perspective one would expect property prices to
        fall. The equilibrium sorting model, however, shows that that logic is incomplete
        and results in an erroneous conclusion regarding the price impact of the policy.
        There are two key factors at play. First, households can move between
        jurisdictions. Accordingly, while a reduction in demand from the residents of a
        desirable area has the immediate effect of pushing down prices, those same price
        falls will encourage households from other jurisdictions to move into the area
        driving up demand and, as a result, prices. Second, the endogenous public good
        responds to changes in neighborhood composition and tax revenues. As a result, a
        policy that initially stimulates relocation can alter the relative provision of
        public goods across neighborhoods, a change that in turn can drive secondary
        demand and price adjustments. As demonstrated by our simulations, in an area where
        public good provision rises, housing becomes more desirable and those demand
        increases act so as to drive prices upwards. Perhaps unexpectedly, despite policy
        reform constituting a significant (20%) reduction in federal government spending,
        within our simulation the knock-on effects of a policy capping MID at 28% actually
        precipitates general welfare increases for households in our simulated population.
        The endogenous tenure choice aspect of our model allows us to explore the impact
        of the policy change on patterns of renting and owning. Our model suggests that
        the key driver of the welfare increase provided by the 28% cap is the fact that a
        policy which increases mortgage costs for high-income households has very little
        impact on their demand for housing or homeownership. Consider the final column of
        Table 5, the rise in public good provision leads to utility gains for almost half
        of the households in the lowest tax bracket and the majority of households in the
        second to fourth income brackets. Moreover, despite being most directly and
        adversely affected by the cap, 78% of households in the 5th and 6th income tax
        brackets experience gains in utility, primarily through the increased local public
        good provision. Table 6 presents a summary of the monetized changes of the policy
        in terms of the federal budget deficit, mortgage interest payments, landlords'
        rents and households' willingness to pay. Willingness to pay is calculated as the
        sum of the amounts of money that each household would pay, or would require in
        compensation, in order to leave them indifferent between their original position
        under MID and that after the policy change. In addition to providing a 20%
        reduction in the deficit, the 28% cap leads to a rise in mortgage interest
        payments and substantial gains in household welfare.

        20.3% refundable flat-rate tax credit

        A seemingly more progressive reform of MID would be to replace the current system
        with a refundable flat-rate tax credit. Under this policy, rather than being able
        to claim MID against income tax, the federal government reimburses all homeowners
        a fixed percentage of their mortgage interest payments. To maintain comparability
        with the MID cap reform discussed in the last section, we consider a refundable
        tax credit of 20.3% which leads to the same overall deficit reduction as the cap.
        In contrast to capping MID, the introduction of a tax credit has immediate
        implications for all households. In the absence of any other adjustments, the
        marginal cost of purchasing housing reduces for households in the lowest two tax
        brackets and all non-itemizers. For itemizers in the top four tax brackets the
        marginal cost rises. For the top tax brackets, the MID cut is more severe than
        under the cap (down to 20.3% compared to 28%). Accordingly, as in the case of the
        cap, the reduction in MID leads to a contraction in housing demand amongst
        previous owners in the top tax brackets. At the same time, demand from households
        in the 2nd and 3rd tax brackets expands. Most interestingly, in jurisdiction B
        expanding demand from households in the 2nd and 3rd tax brackets forces lower
        income households out of homeownership, leading to a reduction in the
        homeownership rate to 66% and a rise in the number of house units per homeowner in
        B (see Table 5). This effect is partially a product of the minimum house sizes
        that must be purchased to reap the gains from homeownership under the chosen
        functional form, in addition to the higher cost of owning relative to renting per
        unit of housing. Lower income households taking advantage of the tax credit also
        stimulates demand for homeownership in A, offsetting the contraction in demand
        from higher income households. The homeownership rate remains stable at 75% and
        the average number of housing units per homeowner falling only slightly from 1.95
        to 1.86. Moderate rises in tax revenues combined with an increase in the median
        income in jurisdiction A lead to small gains in public good provision with school
        quality rising by 1% in both A and B. This increased public goods provision
        provides some compensation for households in light of the higher cost of housing.
        The flat-rate tax credit stimulates changes in the tenure and location choice of
        almost 6% of the population. The progressive nature of the policy makes it
        unsurprising that the majority of the benefits are focused upon the lowest three
        tax brackets. What is surprising, however, is that a smaller proportion of
        households in the second and third income tax brackets benefit from the tax credit
        in comparison to the 28% cap. In addition, more substantial increases in the cost
        of housing result in losses for 66% of households in the top three income tax
        brackets. As can be seen in Table 6, the flat-rate tax credit produces large
        reductions in welfare through higher costs of housing for renters and previous
        itemizers in the top four tax brackets; however the reform also leads to a
        reduction in total mortgage interest payments as overall homeownership rates
        decline. In comparison to the 28% cap, the flat-rate tax credit provides utility
        gains to a smaller proportion of households in every tax bracket except the 2nd
        and from a Kaldor–Hicks perspective the flat-rate policy is inferior to the 28%
        cap.

        4.2% income tax rebate

        Consider next a policy that removes MID and uses the money saved first to reduce
        federal expenditure (by 20% to maintain comparability with the 28% cap) and second
        to reduce income taxes by cutting all household's tax bills by 4.2%. For non-
        itemizers and renters, the design of this reform is potentially positive. Their
        lower income tax liability opens up the possibility of consuming larger properties
        or relocating to A to enjoy relatively higher levels of public good provision. For
        homeowners, the immediate impact of the reform depends on their taxable income.
        Households in the lowest tax bracket do not pay income tax and, as such, are not
        immediately affected by the policy reform. The characteristics of the new
        equilibrium are presented in Tables 4 and 5. Overall, mean owned property size in
        B falls slightly as new owners purchase smaller properties than existing owners.
        The reform motivates a number of households to relocate from A to B in order to
        benefit from the relatively cheaper housing. This leads to an increase in the
        median income in both A and B and higher local tax revenues, supporting an
        increase in local public good provision. As a result, purchase prices rise by 1.5%
        to $7482 in A and 1.26% in B to $5564 as low income households (those in the first
        and second income tax brackets) enter the purchase markets. In jurisdiction B,
        higher housing demand increases homeownership by 1% (column 8, Table 4). However,
        lower demand from existing homeowners is not offset by the rise in price and
        increase in rental demand, as a result lower tax revenues contribute to a slightly
        decreased provision of endogenous public good in both jurisdictions. Despite its
        seemingly regressive design, this policy increases utility for the majority of
        lower income households. For many higher income households, the utility benefits
        of the income tax cut are outweighed by the loss in MID. Indeed, the proportion of
        households in the top four income tax brackets who gain from this policy reform is
        lower than under the 28% cap.27 Finally, considering Table 6, the income tax
        rebate reform increases mortgage interest payments and landlord's rental revenues,
        but creates moderate net reductions in welfare, relative to the other reforms,
        through the higher housing costs that are inflicted on wealthier households.

        $3620 new owner scheme

        This final policy reform replaces MID with a new owner scheme that pays a lump sum
        of $3620 to new homeowners. Again, this is revenue equivalent to the 28% cap. The
        characteristics of the new equilibrium under this policy appear in the final rows
        of Tables 4 and 5. As with the other reforms, the removal of MID has the immediate
        effect of contracting housing demand amongst existing homeowners. The introduction
        of a New Owner Scheme, however, stimulates entry into homeownership amongst
        previous renters in the lowest tax bracket (as can been seen in columns 2 and 4 of
        Table 5). Simultaneously, the New Owner Scheme increases total housing demand and
        leads to a rise in purchase prices in both jurisdictions, rising by 15.2% in A and
        by 17.1% in B (column 3, Table 4). In turn, we observe decreases in the average
        units of housing demanded in the purchase markets, an increase in the average
        units of housing in the rental markets and substantially higher tax revenues in
        both jurisdictions. Despite relocation between A and B reducing median incomes in
        both jurisdictions, the provision of endogenous public goods rises by 2% in A and
        B (column 11, Table 4). Accordingly, previous homeowners who lose the MID are
        compensated in two ways: first, since property prices rise, they benefit from
        capital gains and second, they benefit from increased levels of public good
        provision. While focusing on new owners, this policy reform results in welfare
        gains for households in the first three income tax brackets. The key pathways
        through which those gains are delivered is by supporting the movement of lower
        income households into homeownership and increasing property values and local tax
        revenues, thus facilitating a greater provision of local public goods. Despite
        this, the policy represents the greatest reductions in utility for homeowners in
        the top two income tax brackets: these households face the complete removal of MID
        and are ineligible for the New Owner Scheme. In addition, persisting renters face
        welfare losses as a result of higher house (rental) prices. Returning to Table 6,
        we observe that the New Owner Scheme produces large reductions in landlord's
        rental revenues and household welfare.

<h>DISCUSSION</h>
----------

This paper contributes methodologically to the existing equilibrium sorting literature by
developing a model that incorporates an explicit endogenous tenure decision as well as
endogenous local public goods. These innovations extend the range of policy problems to
which ESMs can be applied to include those where tenure choice and the impact of policy
reform on rates of homeownership are central. Moreover these innovations allow us to
account for the influence of capital gains and housing stock constraints on the
distribution of welfare changes. A simplified model was calibrated using real world data
to examine the possible consequences of reforms to the policy of MID in the U.S. This
exploration begins to shed some light on the complex patterns of change that such reforms
may precipitate in the property market and provides insights that help to inform some of
the more acrimonious disputes surrounding the debate over MID reform. With regard to that
debate, the calibrated simulations show that the impact of removing MID depends crucially
on the nature of the policy that takes its place. First, consider the argument that MID
inflates property prices making homeownership less affordable (Glaeser and Shapiro, 2002).
The simulation results suggest that while MID disproportionately reduces the cost of
purchasing housing for higher income households, we do not find evidence to suggest that
reforming MID would necessarily lead to reductions in house prices. To the contrary, our
simulations indicate that entry into homeownership and greater public good provision could
lead to rising property prices. Second, supporters of MID argue that removing the policy
would damage homeownership rates. This is where the key innovation of our model, the
introduction of endogenous tenure choice, enables us to make a significant contribution to
the policy debate. Our simulations suggest that the impact of reform on homeownership may
be positive or negative. Indeed, for the cap, income tax reduction and New Owner Scheme we
predict increased homeownership rates as new incentives for homeownership are introduced.
Furthermore, despite the fact that the model accommodates changes in tenure as the
relative costs of renting and owning change, we predict quite small changes in
homeownership rates for the cap, flat-rate credit and the income tax rebate. Third,
critics of MID argue that it subsidizes excessive housing consumption amongst wealthy
households, suggesting that the removal of MID would lead to a contraction in the average
property size of owners in the top tax brackets. As with the homeownership rate, our
simulations suggest that the nature of the policy reform has a strong influence on the
mean property sizes demanded by homeowners in each income tax bracket. Contrary to
previous predictions, however, in the cases of the 28% cap and the income tax rebate the
mean property size demanded by homeowners in the top income tax bracket remains the same.
In the cases of the flat-rate tax credit and New Owner Scheme, our conclusions are
consistent with a reduction in the average purchased property size for households in the
top income tax bracket.

<hs>  Model sensitivity</hs>
  ~~~~~~~~~~~~~~~~~

The model presented in this paper provides a tool for analyzing policy reforms and
exploring the types of market adjustments that would characterize the resulting
equilibria. It is important to acknowledge that the calibrated model approximates many
dimensions of the joint housing, tenure and location decision that are not well
understood. To test the robustness of the simulation results, and to identify the most
influential parameters we explored a variety of parameter values for i) the endogeneity of
local public good provision, ii) the specification of housing supply, iii) the degree to
which rental and owned property markets are connected, iv) household preferences, and v)
the tax incidence of property taxes for renters. For the purpose of conciseness a
selection of these results, exploring the first two points, is presented in Table 7,
further results are available from the authors upon request. Table 7 compares three
specifications of local public good provision; i) calibrated feedback via local
homeownership, ii) state level homeownership as a proxy and iii) an inverted calibration
of the feedback effects, alongside two specifications of the housing supply function; i)
fixed short term housing supply and ii) Cobb–Douglas housing supply function with
elasticity of one. Across the range of calibrated parameter values, including those not
presented in Table 7, we find consistent patterns of change in homeownership rates,
predominantly with increases in homeownership rates being achievable through a deficit
reducing policy reform. This is consistent with Shapiro and Glaeser's (2003) assertion
that MID subsidizes households who would be homeowners even in the absence of the policy.
Likewise, our simulations consistently demonstrate that increases in public goods
provision under several of the reforms serve to compensate households for the reduction in
federal spending; the magnitude of this compensation is sensitive to the value of
preferences for public goods, α. Nonetheless, despite this sensitivity, our results
consistently suggest that the proposed 28% cap leads to utility gains for the majority of
households and would be supported, from a utility perspective, by the majority of
households. Moreover, our results suggest that the benefits of the policy would be quite
broadly distributed across the income tax distribution (see columns 8–13 of Table 7). In
contrast, the impacts of MID reform on property prices and the average property size of
homeowners are sensitive to the calibration of the model. In the simulation results
presented in Section 4 we find that property prices do not decrease and the average
property size of owners in the top tax brackets decreases. This finding is quite robust
for the cap, income tax rebate and New Owner Scheme. However, for the flat-rate tax credit
and in calibrations where either rental and purchase markets have been defined
independently or renters do not face the full property tax burden, the model predicts that
property prices could fall (consistent with the argument made by Bourassa and Yin, 2008)
and the average property size amongst homeowners in the top tax brackets could increase
under the 28% cap, flat-rate tax credit and income tax rebate reforms.

<hs>  Concluding remarks</hs>
  ~~~~~~~~~~~~~~~~~~

Examining a range of alternative policy reforms demonstrates the importance of policy
design and the role of path dependency in shaping the outcome of those reforms. With
regard to the latter, there are three key mechanisms at work. First, owning a property
shields high-income households against rises in property prices and subsequently enables
them to channel benefits through capital gains. Second, housing stock constraints fix the
current capital stock of housing making it unresponsive to price changes, these
constraints act to suppress price falls and stabilize homeownership in the face of
contracting demand. Third, endogenous public goods can act as a mechanism for compensating
households. As a result, the complex patterns of change precipitated by policy reforms in
the property market can have quite unanticipated results. Policies designed to be
progressive, such as the tax credit reform, may do less to benefit poorer households than
those that appear to be regressive, such as the income tax reduction reform. Likewise,
policies that economists would normally assume to have excellent efficiency improving
qualities, such as the income tax reduction reform, may lead to significant net welfare
losses. Taken as a whole, our investigation suggests that several reforms to MID could
maintain the prevailing levels of homeownership while delivering more public goods and
contributing to a reduction in the federal deficit. Of course, these results relate to the
calibration of a simplified two-community problem. Given our results, it would be
interesting to see future work directed towards the estimation of a large-scale model with
more formally quantified social returns to homeownership. With these extensions it would
be possible to simulate economy-wide responses to the proposed reforms. Nonetheless, our
results demonstrate the usefulness of the modeling framework and provide important
insights into the broader implications of reforming MID.


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<ART>Exporters, importers and credit constraints
===========================================

Authors: Mirabelle MuÛls
DOI: 10.1016/j.jinteco.2014.12.003
Year: 2015  |  Pages: 333-343
ASJC codes: 2002, 2003
Keywords: Credit constraints, Exports, Firms' heterogeneity, Imports, International trade, Margins of trade

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper analyzes the interaction between credit constraints and trading behavior, decomposing trade in extensive and intensive margins. I construct a unique dataset containing firm-level trade transaction data, balance sheets and credit scores from an independent credit insurance company for Belgian manufacturing firms between 1999 and 2007. Firms are more likely to be exporting or importing if they enjoy lower credit constraints. Also, firms that have better credit rating export and import more. Importing and exporting behaviors differ in how both the level and growth of the various margins of trade are related to credit constraints in one important dimension. In the case of exports, it is the intensive and extensive margins of exports in terms of both product and destinations that are significantly associated with credit constraints whereas for imports it is the extensive margin in terms of products only.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

When the economy enters a recession and a credit crunch shakes the financial sector, or
simply when they suffer other types of shocks, firms might find it harder to access
credit. This is likely to affect their operations, the investments and R&D they conduct
and the way they develop and expand. There is however little empirical evidence on how
important financial considerations are for the international expansion and activities of
firms and on how they adjust their trading activities. This paper considers the
determinants of firm trading patterns by matching firm-level trade transaction data with
individual, time-varying credit ratings. In particular, it seeks to analyze the
interactions between financial or credit constraints on the one hand and exports and
imports margins on the other. While the analysis of firm-level trade has mostly focused on
the relationship between trade and productivity, this paper contributes to a recent
literature studying another critical determinant of trading decisions: the financial
situation of the firm, and in particular the credit constraints it faces. On the one hand,
a bad financial situation might make its suppliers based abroad less willing to risk
trading with the firm, hence affecting its imports. On the other hand, being credit-
constrained would prevent the firm from overcoming any fixed costs associated with either
exporting or importing. Based on a unique and detailed dataset, I find that firms that
enjoy lower credit constraints and bankruptcy risk are more likely to be exporting. Firms
that have better credit rating also export more. They have higher extensive margins: they
export more products to more destinations. Their intensive margin, the average export
value per firm-product-country observation for all combinations with positive exports, is
higher too. The same patterns hold for imports except that the country extensive margin
and the import intensive margin, are not correlated with credit constraints. Finally, most
of these results are shown to hold over time, when estimated with the growth of the
various trade margins. This brings novel insights on the differences between import and
export choices, and these correlations are useful to guide future theoretical work. The
detail of the datasets used is particularly suitable for the questions addressed. First,
the trade and balance sheet data cover the full sample of Belgian manufacturing, at the
firm level, with detailed information on trade participation, but also on the destinations
or origins and products traded. This allows for a full decomposition of trade flows into
the intensive margin as well as firm, country and product extensive margins and the
density of trade. Using firm-level analysis in this paper allows a better understanding of
how firms vary within a given sector. Second, the measure of credit constraints used is
unique in its kind: a yearly measure of the creditworthiness of firms established by an
institution external to the firm. By assessing financial constraints with a continuous
credit rating rather than single and extreme default payment episodes implies that the
effects identified do not only hold in the case of extreme credit constraints. The paper's
main contribution is to be using a measure of credit constraint that exhibits sufficient
within-firm variation over time to relate it to the firms' importing and exporting
outcomes after controlling for firm fixed effects. This paper contributes to two related
areas of the literature. First, the relation between liquidity constraints and exports has
been studied both in theory models and empirically. The next section will discuss relevant
theoretical papers. Empirically, the question has also been studied using different
datasets. Several papers use the sector-level Rajan and Zingales (1998) measure of
“external finance dependence” to examine how it affects exports. Manova (2008) shows how
financial frictions and credit market development explain cross-country patterns of trade
at the sector level. Export growth is proven to be slower in external finance dependent
sectors in Iacovone and Zavacka (2009). Considering Belgian exporters as in this paper,
Behrens et al. (2013) find that imports fell more during the recent recession for firms
with above median reliance on external finance. Analyzing transaction-level data and the
financing terms used by firms, Antràs and Foley (2015) show how trade finance, and hence
financial constraints, influence the impact of macroeconomic and financial crises.
Analyzing monthly US imports from countries with varying degrees of credit market
tightness, Chor and Manova (2012) demonstrate that exports are less sensitive to the cost
of external capital in industries relying less on external finance or less financially-
vulnerable according to other measures, and that this sensitivity rose during the
financial crisis.1 Albornoz et al. (2012) analyze the sequential pattern of exports
expansion by successful new exporters for Argentina and find that credit constraints do
not explain these patterns.2 The firm-level dimension of the dataset I use allows me to go
beyond this type of sectoral analysis and exploit intra-sector variations. Others have
used firm-level measures to capture credit constraints. Minetti and Zhu (2011) analyze a
cross-sectional survey of Italian manufacturers and find that “credit rationed” firms are
less likely to export and are likely to export less. They focus on the firm extensive
margin of exports. Berman and Héricourt (2010) find similar results for developing
countries, using financial ratios as measures of constraints. They find that financial
constraints are not correlated with export values or export survival in those countries.
Other authors also explore these questions by deriving measures of financial health and
constraints from balance sheet financial ratios. Greenaway et al. (2007) find no ex-ante
effect on the probability of becoming an exporter while Bellone et al. (2010) do. Askenazy
et al. (2011) find that credit constraints negatively affect the entry into a new
destination and increase the probability of exiting a market.3 Exploiting data available
from the international firm-level data from the World Bank Enterprise Surveys, Wang (2011)
reports that the probability of exporting and the export volume increase with age, which
is consistent with the hypothesis that firms need to accumulate sufficient collateral
before they can borrow enough funds to profitably export. This paper extends this
literature by analyzing the extensive margins at the level of destinations and products as
well as considering financial constraints as a continuous measure. A second area of the
trade literature has empirically analyzed firm-level imports. The fact that the import of
new varieties leads to higher productivity and growth has been shown empirically both at
the country level (Broda and Weinstein, 2006) and at the firm level, with imports of
intermediates or reductions in input tariffs being associated with productivity gains or
higher productivity levels (see Antràs et al. (2014); Amiti and Konings (2007); Kasahara
and Rodrigue (2008) or Goldberg et al. (2010)). While my results do not contradict these
findings, the question I address is whether financial constraints might prevent some firms
from reaping the benefits of importing intermediates. Although it may appear surprising
that financial constraints shape the country-level extensive margin differently on the
export side and on the import side, these results are consistent with the findings of
Antràs et al. (2014). These authors show that the determination of the country-level
extensive margin of importing is much more complicated than in models of selection into
exporting, mainly because the marginal increase in profits from adding a country to a
firm's set of potential sourcing locations depends on the number and characteristics of
other countries in the set. Imports and exports have often been compared in the recent
analysis of firm-level trade data. Descriptive evidence by Bernard et al. (2007), Muûls
and Pisu (2009) or Halpern et al. (2005) shows that importing firms share many attributes
with exporters: they are both larger and more productive and product and country-level
patterns of trade at the firm level are similar for both. Based on a theoretical model
estimated with Chilean data, Kasahara and Lapham (2013) analyze the complementarities of
exports and imports for the productivity and welfare gains of trade. This paper shows that
imports and exports are different in some important dimensions when put in relation with
credit constraints. The remainder of the paper is organized as follows. Section 2 presents
the conceptual framework of how financial constraints can affect exporting and importing
patterns. Section 3 describes the data, and demonstrates in particular why the Coface
score is an appropriate measure of credit constraints. Section 4 contains the empirical
analysis of the links between export and import patterns and credit constraints at a given
point in time, while Section 5 takes a closer look at trade growth. Section 6 concludes.

<h>CONCEPTUAL FRAMEWORK</h>
--------------------

Why are credit constraints analyzed here specifically in relation to trade transactions
and not both domestic and international activities? External finance is indeed used by
firms to finance investments in capital, product development and R&D or advertising among
others. However, in addition, trading firms face incremental fixed and variable expenses
thus needing even more access to external capital. In order to frame the empirical
analysis below, one can decompose total trade flows. What are the impacts of credit
constraints on these different export margins that are predicted by the existing models?
Focussing mainly on a framework with only a firm level extensive margin as in Eq. (1),
Chaney (2013) and Manova (2013) introduce credit constraints in a theoretical model of
trade with heterogeneous firms à la Melitz (2003) and yield several predictions on the
equilibrium relationships between productivity, credit constraints, exports and export
margins. In both models, firms must pay up-front a fixed cost of entry into foreign
markets and hence need sufficient liquidity to do so. In Chaney's model, firms finance
these costs with cash flows from their domestic operations. Once a firm has entered
foreign markets, financial constraints do not impact the marginal cost of exporting: the
firm will finance an increase in the scale of its exports through its internal cash-flow
and foreign trade credit. In equilibrium, financial constraints impact the extensive but
not the intensive margin of exports. In Manova (2013), firms need to borrow to cover both
the fixed and the variable costs of exporting. This follows from the imperfect
enforceability of international transaction contracts together with imperfect information
on the potential returns from foreign markets. In equilibrium, total exports will increase
with lower credit constraints. More productive firms and less credit-constrained firms
will be more likely to export. Credit constraints will decrease the firm extensive margin
and the overall intensive margin vt (average exports per firm). To summarize, these models
illustrate that in equilibrium, credit constraints affect the intensive (respectively,
extensive) margins of exports if financial constraints are assumed to affect the variable
(respectively, fixed) costs of exporting. There is to the best of my knowledge no model
that explicitly considers firm exporting decisions in relation to credit constraints with
a distinction of export margins according to Eqs. (2) and (3).5 In a stylized dynamic
model, Besedeš et al. (2014) focus on changes in the intensive margin and show that credit
constraints can have an important role in the start of exporting activity, but not on the
growth of exports in later stages. There is also limited empirical firm-level evidence on
these issues, with existing studies focussing on export margins as defined by Eq. (1), or
considering whether or not the firm exports to more than one market as in Minetti and Zhu
(2011). By illustrating the correlations between these constraints on the one side and the
different extensive margins and the intensive margin of exports on the other, the results
of the empirical analysis below should serve as a motivation for future theoretical work
in this area.

<hs>  The Belgian balance sheet and trade transaction data</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

This dataset provided by the National Bank of Belgium has been used in several papers
analyzing export and import patterns and behavior (see Muûls and Pisu (2009); Behrens et
al. (2013) and Araujo et al. (2012) among others). It merges firm-level balance sheet and
trade data for Belgium. The balance sheet part of the BBSTTD is used to extract firm-level
annual characteristics, including employment, value added, profitability, sector of
activity and to compute total factor productivity. The trade data includes the value,
destinations and origins as well as products at the 8-digit Combined Nomenclature (or CN8)
level of the EU.6 Manufacturing firms only are selected as belonging to sectors 15 to 36
of the NACE-BEL classification.7 The data is then merged into the Coface database,
described in the following subsection. Only firms for which a Coface score is given for
each year a balance sheet was available are included in the dataset. All observations are
kept in the resulting dataset, which is described in Table 3.

     <hss>The Coface score</hss>

        As a measure of credit constraints, I use the Coface Services Belgium Global Score
        for more than 9000 Belgian manufacturing firms between 1999 and 2007. Credit
        insurance firms offer insurance policies to businesses that wish to protect their
        accounts receivable from loss due to commercial and political credit risks such as
        protracted default, overdue accounts, insolvency or bankruptcy. Established in
        France in 1945 as a credit insurance company, Coface is now an international firm,
        providing a range of services to facilitate business-to-business trade. Among
        these, it also provides credit worthiness information: through a worldwide network
        of credit information entities, it has constructed an international buyer's risk
        database on 44 million companies. Data from public and private sources are added
        to Coface's internal data in order to manage each company's rating and Coface's
        risk exposure on a continuous basis. Fig. 1 provides an example of who the parties
        would be in a credit insurance contract. Belgian firm A is a client of Coface. It
        wants to sell a product to Belgian firm B and protects itself against the risk
        that B might default on paying for that product. As it would do for any
        transaction, it asks Coface whether it will be covered. Coface, if it hasn't
        already done so, will compute a score for B, and if it is high enough will insure
        the transaction. A will send the product to B in exchange for payment. If B
        defaults, Coface will pay A and seek to recover the amount from B. Imagine that
        Belgian firm B also exports goods to firm C and imports inputs from firm D.
        Neither B, C nor D are clients of Coface, but because of its transaction with firm
        A, the credit rating score of firm B will be in the dataset. There is a large
        academic literature on bankruptcy prediction models such as that used to construct
        Coface's score (see for example the review by Balcaen and Ooghe (2006)). However,
        privately-computed probability of default or credit scores such as Coface's are
        naturally less well-known. Various datasets are compiled to construct the Coface
        score: the firm's financial statements (leverage, liquidity, profitability, size,
        etc.), its legal form, age and life cycle, location and information on its
        commercial premises as well as industry specific information. Data on payment
        incidents both with other firms and to the social security (ONSS) are also used.
        Finally, legal judgments and the board structure are taken into account. For
        example, if a firm goes bankrupt it will negatively affect the score of all
        companies that have common board members. These various inputs are combined using
        several statistical methods and trial-and-error. The result is a score ranging
        from 3/20 to 19/20. Although the model predicts continuous scores they are rounded
        to unity in the obtained data. The score therefore contains information about the
        firm's quality, performance and productivity. However, two firms with equally
        valuable projects, and identical profitability and productivity can be very
        different in terms of financial health, board structure, and other elements that
        will determine their score and their access to credit. The empirical analysis will
        therefore control for a number of variables that could potentially influence both
        the Coface score and the trading activity, such as size, profitability and
        productivity of firms.8 A firm's score varies from year to year: the average
        yearly change is 2 points (or 12.5% of the largest possible variation from 3/20 to
        19/20) with a standard deviation of 2. The average difference between a firm's
        largest score over the time sample and its lowest is 6 points. It is this
        variation that I exploit in my analysis below. Importantly for the purpose of this
        paper, Coface's score does not include in its determination model any information
        on the firm's exports or imports. Firm-level trade data is not public information
        in Belgium and even if Coface would have such information for some firms through
        it's network of international clients, it does not enter directly in the
        computation of the score. However, trade performance might affect the score
        indirectly, through its impact on profitability for example or other variables
        that are included in the construction of the score. While it does not remove all
        potential endogeneity in the Coface score, great care is taken in the remainder of
        the paper to include crucial firm-level controls and to exploit the panel
        dimension of the data. Constructed as a bankruptcy risk measure, the score is
        highly correlated with how credit-constrained a firm is, reflecting the same type
        of information that a bank would use to decide whether it lends to a firm. Being
        determined independently by a private firm, it is unusual for such data to be
        available and has a great advantage on measures of credit constraints used in the
        literature so far: it is firm-specific, varies through time on a yearly basis9 and
        allows for a continuous measure of the degree of credit constraint rather than
        classifying firms between two constrained or unconstrained categories. Compared to
        datasets on payment incidents that would identify a small subset of firms as being
        credit-constrained,10 the Coface score ranks firms along the whole spectrum of
        ratings. Payment incidents would only be one of the elements affecting the score,
        in combination with many others. Overall, the Coface score is a well-suited direct
        measure of creditworthiness used by other firms and by banks when extending loans,
        and I therefore use it in my empirical analysis to measure how credit-constrained
        firms are.

     <hss>External validation</hss>

        This section presents the correlation between the score and firm fundamentals. It
        also relates it to the important literature on credit constraints, in particular
        in corporate finance. Given the methodology used to construct the score is not
        available publicly, it is shown here how correlated the score is with the firm's
        financial situation and productivity. A selection of financial ratios11 measures
        each firm's solvency and investment. Table 1 shows how strongly the Coface score
        is correlated with the financial situation of the company, in particular its
        solvency and investment intensity. Firm and year fixed effects are included in the
        OLS regression, thus also controlling for possible differences in, for example,
        risk premie across industries and years which might affect the Coface score and
        other financial measures differentially. Solvency is measured with two ratios:
        financial independence and coverage of borrowings by cash flow. The strong
        correlation between these and the score shows that firms that are more able to
        meet their short- and long-term financial liabilities have a higher score.
        Financial independence, the ratio between equity capital and total liabilities,
        reflects how independent the firm is of borrowings. The coverage of borrowings by
        cash flow measures the firm's repayment capability, and its converse specifies the
        number of years it would take to repay its debts assuming that its cash flow was
        constant. Higher scores are also associated with larger investment ratios, the
        acquisitions of tangible fixed assets over value added. EBITDA (Earnings before
        Interests, Taxes, Depreciation and Amortization) is a commonly used financial
        measure of the operational profitability and performance of the firm. It appears
        as being positively associated with the Coface score. I will include it as a
        control in the regression analysis below, in order to control for the effects of
        the profitability of a company. Productivity has been shown to be an important
        determinant of trade patterns. It is measured here as in Levinsohn and Petrin
        (2003).12 Column (5) of Table 1 reports a positive but not perfect correlation of
        the Coface score with productivity, confirming that credit constraints and
        productivity are two different issues to be considered when analyzing export
        behavior. The effects of financial constraints on firm behavior are an important
        area of research in corporate finance. Compared with the existing literature, the
        Coface score provides many advantages, as described above. One of the many
        approaches in the literature consists of sorting firms into financially-
        constrained and unconstrained types on a yearly basis by ranking firms according
        to different measures. In Almeida et al. (2004), firms in the top three deciles of
        their payout dividend ratio would be considered as less financially-constrained
        than firms in the bottom three. Allayannis and Mozumdar (2004) use total assets. I
        test in Table 2 whether the score is consistent with such classifications. The
        mean Coface score, its standard error, maximum and minimum observations are
        reported separately for constrained and unconstrained firms. Firms whose dividend
        payout is in the top 30 percentiles are considered as financially unconstrained,
        whereas those in the bottom 30 percentiles are financially constrained. The same
        is done with total assets. The mean test is passed, meaning that constrained firms
        have a lower score than unconstrained firms, in both criteria. It is robust to
        using only one cross-section of the data, or taking out observations within the
        top and bottom percentiles of each measure. This confirms that the Coface score
        offers a creditworthiness measure that is consistent with other measures used in
        the literature.

<hs>  Export or import status</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

I begin the empirical analysis by exploring the variation in credit scores between
exporters and importers on the one hand and non-traders on the other. It appears that less
credit-constrained firms are more likely to be trading. This is shown at first in the
descriptive statistics presented in Table 3: on average, traders are not only
significantly larger and more productive, they also have a significantly higher score,
meaning they are more creditworthy and less liquidity-constrained. Where
Ex/Importer(0/1)i,t is a dummy that takes the value 1 if firm i is an exporter/importer at
time t and zero otherwise. CSi,t − 1 is the Coface credit score13 for firm i at time t − 1
and additional firm characteristics are added: productivity, operational profitability,
wage, age, employment, MNE status and financial ratios proxying firm access to finance. Of
course, many other factors might affect a firm's export status such as the current
economic situation, and other characteristics of the firm. Other potential factors such as
exchange rates, factor endowments, factor prices or industry demand will be common to all
exporters of a sector in a given year. This is why I include firm and sector-year fixed
effects in my specifications, denoted by {FE}, thus eliminating any bias that they could
cause. The results are also presented with an alternative set of fixed effects – year and
sector – for comparability with the previous literature. Each firm only belongs to one
sector so in the specification where firm fixed effects are not included, sector fixed
effects are used to control for non-time-varying sector-specific idiosyncrasies. Including
fixed effects, controlling for firm-level observables and given the composition of the
score described above, the residual effect of the Coface score is a good measure of credit
constraints faced by a firm. Given the number of fixed effects to be included in the
specification, using a linear probability model in levels addresses the incidental
parameter problem that affects non-linear fixed effect estimates. This specification is
used in Bernard and Jensen (2004) for a very similar binary choice problem despite the
problems this might provoke (e.g. predicted probabilities outside the 0–1 range). The
first four columns of Table 4 only include sector and year fixed effects, as in Bernard
and Jensen (2004). In columns (5) and (6), the full set of sector-year and firm fixed
effects are included. Finally, as a robustness check, the results using a conditional
logit estimator with year and firm fixed effects are presented in column (7). Other firm
characteristics are also included as controls in columns (3) to (7): operational
profitability, wage levels, age of the firm, multinational status and the financial ratios
presented in Table (1). As would be expected, the Table shows that more productive firms
are more likely to export, although the coefficient becomes insignificant once firm and
sector-year fixed effects are included. The coefficient on the lagged credit score is
positive and significant in all specifications, confirming that firms which are less
credit-constrained have a higher probability of being exporters. In column (2), the
coefficient on productivity is not reduced compared to the first column, indicating that
the score captures the additional effect of credit constraints. Column (3) shows that the
effect of productivity decreases while that of the credit score increases when more
controls are added. When including the lagged export status variable, as in Bernard and
Jensen (2004), the coefficients on TFP and the Coface score are strongly reduced as shown
in column (4). Columns (6) and (7) show that the sign and significance of the score
coefficient remain robust to including firm as well as sector-year fixed effects.
Conditional logit with firm and year fixed effects yields similar results although the
significance of the coefficient on the Coface score is lower, as shown in Column (7).
These results are consistent with the literature showing that the firm extensive margin of
exports (fm in Eq. (1)) is positively correlated with lower credit constraints. Very
similar results are obtained when estimating the effect of the Coface score on import
status using exactly the same specifications. As shown in Table 5, one notable difference
with export status is that the positive effect of productivity on the probability of being
an importer remains strong and significant across the different specifications. Less
financially-constrained firms have a higher probability of being importers. Also, the
strongly significant coefficient on the Coface score is robust to including sector-year
and firm fixed effects as well as the lagged importer status in the linear probability
model as shown in column (6) or the conditional logit specification in column (7). The
coefficient of the credit constraint score is larger than in the case of exports. Import
and export status, and hence the firm extensive margins for both trade flows, are
therefore correlated to credit worthiness in a very similar way. These first results show
that there are factors of credit worthiness that the Coface score integrates, over and
above the observed balance sheet firm-level variables that are included as controls and to
which the score is correlated. The regressions here and in the next sections are
highlighting the effects of these additional elements of credit worthiness.

<hs>  Value, destinations, origins and products</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In order to obtain a sense of the magnitude of these effects, one can compute that a one
standard deviation increase in the log of the credit score corresponds to a 4.4%14
increase in total exports. This can be compared to the average annual increase in total
Belgian exports between 1995 and 2008 which was 5.4% (Baugnet et al., 2010). Comparing the
different margins, a 10% increase in the score (and not the logarithm of the score) would
correspond to a 0.4% increase of both the number of products exported and destinations
served and a 0.45% increase of the intensive margin. This is a small figure in the case of
products given that the mean annual increase in the number of products exported by a firm
in the dataset is 6.5%. It is however a much larger result for countries given that on
average firms do not increase the number of countries they export to. In the case of
imports, the lagged score is positively and significantly associated with total imports as
well as the number of products imported, the product extensive margin. But in contrast
with the corresponding result for exports, the coefficient on the number of origins is
insignificant. A potential explanation behind this result is that firms rarely source
goods from multiple countries. The mean number of countries from which a firm imports a
given product, whether defined at the 8-digit or 6-digit level, is 1.5, while it is 3.68
countries per exported CN8 product. This has also been found using U.S. data in Antràs et
al. (2014) and it could be due to the fixed cost of expanding on the product extensive
margin of imports being smaller than the fixed cost of expanding on the country extensive
margin. The fact that the country-level extensive margin of imports is not significantly
shaped by the credit score is also consistent with the model in Antràs et al. (2014).
Another channel to take into account is that if a firm does not have a good financial
health, foreign firms will be less willing to risk a payment default, limiting the range
of inputs it can import from abroad. There appears to be no relationship between the
import intensive margin and credit constraints, which would indicate that variable costs
for imports are less related to the access to external finance. One standard deviation
increase in the logarithm of the score would correspond to a 3.4% increase in total
imports, suggesting that access to credit matters less than in the case of exports on
aggregate, although the coefficient for the product extensive margin is slightly higher
than for exports. These various results will be analyzed in their growth dimension in
Section 5. It is also interesting to note that for exports, only total value and the
intensive margin are positively related to productivity while for imports, it is also the
case of the number of origins. A higher EBITDA is positively associated with all margins
for both imports and exports. This suggests that firms that reach a certain maturity make
bigger margins on their products thus obtaining higher profitability and exports. A higher
EBITDA might also reflect lower input costs which could be the result of a more intense
importing behavior. The negative and significant coefficients for the financial
independence ratio that appear in most specifications of Tables 6 and 7 could be due to
the fact that a higher ratio at t − 1 will facilitate the firm's potential to increase its
liabilities which in itself will decrease the ratio at t. This decrease has a negative
impact on trade values and its margins. Finally, the strongly significant and large
coefficient for the employment variable in the case of the extensive margins confirms that
it is important to control for firm size when considering the trading decisions of firms.
These results clearly establish the relationship that exists between credit constraints
and exporting and importing patterns, even if once productivity, size, profitability,
access to finance and other firm characteristics are controlled for.

<hs>  Extensive and intensive margin for exports</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

I found in Section 4.2 that firms with a higher credit score are also likely to display
higher values of total exports, to be exporting more products, serving more destinations
and to have larger average exports per non-zero product-country. This result also applies
to the growth in total exports and its components, except for the intensive margin. In
this section, I run the same specification as in Eq. (5), but taking as dependent
variables the various elements of Eq. (6). I include firm fixed effects, sector-year
dummies and control for firm characteristics in an OLS specification as above. Levels of
the dependent variable in the previous year are included as explanatory variable in each
case, to capture together with the firm's age the existing exporting activity level
effects on each margin, although the results are robust to excluding them from the
regression. The first column of Table 7 shows that the increase in total exports relative
to the previous year is positively related to creditworthiness. One standard deviation
increase in the logarithm of the score can be associated with a 2.5% increase in the
growth of exports. This can be decomposed into a positive relation with the increase in
the number of destinations served as shown in column (2) and the increase in the number of
products (column (3)). It confirms that credit constraints can be associated with the
fixed costs of exporting to more countries or more products. Variations in the intensive
margin of trade, the dependent variable of column (5), are not correlated with credit
constraints. The coefficients on productivity are not significant when considering the
product and destination extensive margins suggesting that when looking at changes over
time, it is important to also consider other determinants of trading patterns. Besides,
being part of a multinational is positively associated to the increase in the number of
destinations and products exported but not the intensive margin. Finally, the export
levels, whether in value, products or destinations in t-1 are correlated to the total
growth as well as to all three margins negatively: firms are less likely to grow in all
dimensions if they are already strong exporters.

<hs>  Extensive and intensive margin for imports</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Identical specifications are run for imports. There is a strong statistical relationship
between the growth of imports and the Coface score at t-1: an increase of one standard
deviation in the logarithm of the score is associated with a 2.6% increase in the growth
of imports, a figure very similar as that for exports. However, in contrast with the
results for exports when decomposing into different margins, credit worthiness appears to
be strongly significantly correlated with the imported product extensive margin but not
with the growth in the number of countries imported from, as shown in columns (7) and (8)
of Table 7. This suggests that liquidity is not correlated with importing from more
origins, but is positively so with expanding the range of imported inputs. As discussed
above, this correlation suggests the presence of sunk costs of importing an additional
product from abroad. In addition, it could also be related to the default risk reflected
in the score: foreign companies will be less willing to take this risk if the importer has
a lower credit rating. As in the case of exports, changes in average import values per
active product-country are uncorrelated with credit constraints. The coefficients on
operational profitability are positive and significant across all import margins,
including the intensive one. It is also noteworthy that MNE status is not correlated with
import margins. The results in Table 7 reinforce the findings from Section 4.2 that
considered the levels of the trade margins. The lack of association between number of
countries imported from and credit constraints could reflect the fact that contrary to
exports where more destinations imply larger markets, the primary rationale for imports is
the necessity to source inputs that are either not available domestically, or not at the
same levels of price or quality. The novel finding is that at the firm level, the
relationship between credit constraints and the country extensive margin is different for
imports and exports.

<h>CONCLUSION</h>
----------

In this paper, I show that credit constraints are related to export and import volumes and
patterns. A precise and complete dataset on trade transactions at the firm level for the
Belgian manufacturing sector is combined to a unique and very useful yearly measure of
credit constraints faced by firms, a creditworthiness score constructed independently by a
credit insurance company. These allow me to examine the relationship between credit
constraints and trade in a new way. My main contribution is to show that credit
constraints are important across the spectrum, not only in cases of payment defaults and
that they are correlated differently with export and import margins. It is shown that
firms which are less credit-constrained, more productive and profitable have a higher
probability of being exporters or importers. Such firms are also likely to report larger
total trade values. While credit constraints are positively associated with both the
country and product extensive margins and the intensive margin of exports, this is not
true in the case of imports where it is only the case for the product extensive margin of
imports. Finally, this result also holds when decomposing the growth of exports and
imports. I find that the growth in the number of products exported and destinations served
is positively correlated with the Coface score measure. This supports the hypothesis that
entering a new market or exporting a new product imply fixed costs for exporters. On the
other hand, for imports, a rise in its credit score is associated with an increase in the
number of inputs imported by a firm. This might reflect the impact of the firm's financial
situation on both a firm's potential to pay the fixed cost of sourcing an additional input
from abroad, as well as the willingness of its potential suppliers to take the risk it
might default. Related to the fact that a firm rarely imports a good from multiple
countries, I find that a decrease in credit constraints is not positively associated with
an increase in the number of countries that a firm sources its imports from. These results
confirm the link between credit constraints and export and import margins. They also
highlight the potential role of government agencies in reducing the fixed costs of entry
to new markets or of importing new inputs. Exploring further the relationship between
financial constraints and trading behavior, by using firm level information on specific
products' domestic sales versus exports, could shed further light on the links between the
dynamics of trade and financial constraints.


<h>REFERENCES</h>
----------

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<ART>Foreign aid and domestic absorption
===================================

Authors: Jonathan Temple, Nicolas Van de Sijpe
DOI: 10.1016/j.jinteco.2017.07.010
Year: 2017  |  Pages: 431-443
ASJC codes: 2002, 2003
Keywords: Absorption, Common correlated effects, Dutch Disease, Foreign aid

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper introduces a new ‘supply-push’ instrument for foreign aid, to be used together with an instrumental variable estimator that filters out unobserved common factors. We use this instrument to study the effects of aid on macroeconomic ratios, and especially the ratios of consumption, investment, imports and exports to GDP. We cannot reject the hypothesis that aid is fully absorbed rather than used to build foreign reserves or exiting as capital flight, nor do we find evidence of Dutch Disease effects. Aid leads to higher consumption, while the evidence that it promotes investment is less robust.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Although a large literature studies the effects of aid using cross-country regressions,
its problems are well-known. Researchers must contend with the endogeneity of aid, the
high persistence of output, the uncertain determinants of growth rates, nonlinear effects
of aid, biases from measurement error, and the likelihood of substantial heterogeneity in
the effects of aid. Moreover, since aid is given in many different forms and with a
variety of motives, these regressions invite concerns that are not purely statistical. For
its detractors, this literature uses unreliable data to arrive at fragile answers to the
wrong question. These criticisms may seem decisive, but some important questions are hard
to answer without cross-country data. In this paper, we seek to advance the literature in
two ways. First, we introduce a new ‘supply-push’ instrument for aid, to be used together
with an estimator that filters out unobserved common factors, even when their effects
differ across countries. In principle, this combination of instrument and estimator will
identify the causal effect of aid under more general conditions than existing approaches.
It could be applied to a wide range of aid-related questions in future research. Second,
we shift the focus to whether and how foreign aid is absorbed by the domestic economy.
Aid, as a capital transfer, is not part of measured GDP. The aid could be absorbed, by
allowing increased domestic expenditure, but this is not the only possibility. It might be
offset by a corresponding capital outflow, or used to accumulate foreign exchange
reserves. Some of the aid flows recorded by donors will not correspond to international
transfers: for example, some forms of donor-sponsored technical assistance will not have a
direct effect on the recipient's domestic expenditure. In all these cases, aid is not
absorbed by the domestic economy. For absorption to take place, domestic expenditure must
increase relative to domestic production, implying an increase in net imports. Hence, we
begin by examining the causal effect of aid on net imports. We are also interested in how
absorption takes place. Absorption requires an increase in at least one of the components
of domestic final expenditure: household consumption, government consumption, and gross
investment. We study the effects of aid on the ratios of these components to GDP. This
should help us to understand the potential effects of aid. For example, if aid improves
the investment climate, we would expect to see an increase in investment relative to GDP,
and this has been a central concern of the empirical aid literature since its inception.
We will argue that the effects of aid on investment, and other macroeconomic ratios, are
easier to study than the effects on growth. Further, in our empirical work, these effects
will be identified from relatively persistent changes in aid receipts, rather than
transitory and endogenous changes. The well-known identification problem in the cross-
country literature is that aid is not randomly assigned. To address this problem, we
introduce a supply-push instrument. It is based on the idea that the exposure of
recipients to changes in donor budgets varies across recipients. Consider two aid
recipients, A and B, and a single donor. Country A accounts for a larger share of aid from
the donor, and this greater exposure persists over time. In that case, when the donor's
budget increases for some exogenous reason, the movement in aid is larger for country A
than for country B, driven solely by the changing supply of aid. This suggests the
following instrument: we can construct a synthetic measure of aid at each date t, based on
each country's share of aid in a donor budget at some initial date t0, multiplied by the
current donor budget at date t. As an example, consider what happens if the British aid
budget increases relative to the French aid budget. Former British colonies are likely to
see an increase in aid received, relative to former French colonies. More generally, there
will often be long-term connections between particular donors and recipients, so that
recipients are more exposed to variation in some donor budgets than others. Our instrument
uses changes in total donor budgets, weighted by the initial shares of recipients in those
budgets, to isolate exogenous changes in aid receipts that are not driven by the
conditions of individual aid recipients. We call this a supply-push instrument; it is
related to the work of Bartik (1991) on regional economics and Card (2001) on the labor
market effects of immigration. As in the immigration setting, the origins and destinations
of flows of aid are large in number, and this makes it unlikely that the instrument — as a
weighted average of many donor budgets — will be correlated with recipient-specific
conditions. We investigate this further below. A possible objection is that donor budgets
may be influenced by forces common to many recipients. For example, world economic
conditions are likely to affect donor generosity, and also the outcomes of poor countries.
Drawing on recent work in the panel time series literature, global forces can be seen as
unobserved common factors with loadings that differ across countries. We filter these out
using an instrumental-variable version of a common correlated effects (CCE) estimator.
This class of estimators was introduced by Pesaran (2006) and extended to instrumental
variables by Harding and Lamarche (2011). Our paper is the first to apply this approach to
the study of foreign aid. The combination of the new instrument and estimator should mean
that we identify causal effects of aid under more general conditions than the existing
literature. We find that aid is at least partially absorbed, reflected in net imports. We
cannot reject the hypothesis that aid leads to a one-for-one increase in net imports,
corresponding to full absorption. This occurs mainly through an increase in imports rather
than a decline in exports, and hence we do not find symptoms of Dutch Disease. The
findings hold across a range of estimators and robustness checks. There is similarly
robust evidence that aid leads to increases in total consumption. This appears to be
driven by increases in household consumption, but those estimates are less precise unless
we exclude outliers. The evidence that aid promotes investment is weaker. In some models,
aid has a delayed effect on investment, but these results are sensitive to the estimation
method and the exclusion of outliers. The next section will sketch possible relationships
between aid and macroeconomic ratios. Section 3 explains the approach to estimation and
its relation to the literature. Section 4 describes the data. In Section 5, we analyze
whether and how aid is absorbed, and the possibility of Dutch Disease. Section 6 presents
robustness checks, before Section 7 concludes. An appendix describes the CCE IV estimator.

<h>AID AND MACROECONOMIC RATIOS</h>
----------------------------

From a national accounts perspective, foreign aid is a capital transfer which does not
contribute directly to GDP, but in principle allows an increase in domestic expenditure on
final goods and services, relative to domestic production. Alternatively, aid might be
used to accumulate foreign reserves, or lead to a capital outflow. Some aid may be spent
on consultants who work exclusively in the donor country, with no direct effect on the aid
recipient's domestic expenditure. It is therefore interesting to ask whether aid is
absorbed. Domestic absorption is typically defined as the sum of household consumption,
gross investment, and government consumption. We are interested in (1) whether aid is
reflected in higher domestic expenditure on final goods and services, and (2) which
expenditure components are most affected. This helps to clarify what is at stake in the
paper. We show that aid is generally absorbed — it increases expenditure relative to
output — but also find that consumption responds more strongly than investment. We do not
uncover any symptoms of Dutch Disease. These results do not establish whether aid is
‘effective’, a hard task for a single paper, but they do contribute new evidence to the
relevant debates. We first consider what it means for aid to be fully absorbed. Take Y as
GDP, equal to the sum of household consumption C, gross investment I, and government
consumption G, minus net imports M − X. For aid to be absorbed, at least one of C, I or G
must increase, along with their total. If they increase relative to GDP, the GDP identity
implies that the ratio of net imports to GDP, (M − X)/Y, must also increase. There is
nothing problematic about this; it is what must happen if aid permits greater domestic
expenditure relative to domestic production.1 In the short run, if aid is devoted to
higher domestic expenditure on final goods and services, net imports will rise one-for-one
with aid. If the response of net imports is smaller than this, aid absorption is only
partial. To study absorption, we take the ratios C/Y,I/Y,G/Y and (M − X)/Y as our
dependent variables. The way aid is absorbed might differ between the short and the long
run. In the short run, aid might be used to build foreign exchange reserves which are used
to finance higher expenditure only later, so that full absorption is temporarily
postponed.2 More generally, the relationships between macroeconomic ratios and aid could
be complicated over longer time horizons. If aid is spent in ways that improve the
investment climate, the long-run effect of aid on investment could be much larger than the
short-run effect. Or consider what happens when donor funds are spent on consultants
working in the donor country: short-run absorption will be zero, but technical advice may
later be reflected in economic policies and hence in macroeconomic ratios. Our empirical
analysis will distinguish between short-run and long-run effects, by estimating dynamic
models, sometimes with a role for lagged aid. The models we estimate can be related to
macroeconomic theories of the aggregate effects of aid. In the one-sector Ramsey model, a
permanent increase in aid raises the investment ratio in the short run, but not the long
run. Aid promotes faster convergence to the steady-state, but the long-run levels of the
capital stock and GDP are invariant to aid (Obstfeld, 1999). Along the balanced growth
path, all aid is consumed. From a national accounts perspective, consumption is higher
while investment and GDP are unchanged, and the increase in steady-state consumption is
permitted by imports of the final good. When the ratio of aid to GDP increases
permanently, the long-run C/Y and (M − X)/Y ratios increase to the same extent, leaving
the other ratios unchanged. In a two-sector model of a small open economy, with traded and
non-traded goods, the effects are more complicated. Aid may increase or decrease the long-
run capital stock and gross investment, depending on whether traded production is
relatively capital-intensive. Section B.1 of the online appendix discusses this in more
detail. Models with balanced growth paths typically imply that the long-run consumption
and investment ratios are stable functions of structural parameters. In a model with
shocks, there would be a common stochastic trend in consumption, investment and output,
while the long-run ratios would be mean stationary. The long-run ratio of consumption to
output would be linear in the ratio of aid to GDP, where the intercept depends on
structural parameters and can be treated as a fixed effect. By working in terms of ratios
to GDP, we stay close to these predictions and avoid the non-stationarity that would arise
with alternative explanatory variables, such as aid per capita. One drawback is that
scaling our variables by GDP risks inducing correlations between variables that were
originally unrelated. We examine this possibility in detail, including the pattern of
results across the different ratios. We consistently find effects of aid on some ratios
and not others, where the pattern conforms with the predictions of theoretical models, and
where the effect sizes have plausible magnitudes. To generate this pattern, a story based
on spurious correlations might have to be somewhat contrived. Other reasons to be wary of
that explanation include additional results from first-differenced models, and models with
the dependent variable in logarithms and which also include the logarithm of GDP as an
explanatory variable. There are some advantages to studying absorption rather than growth.
First, the relationships between macroeconomic ratios and aid intensity are more likely to
be linear, for the reasons just discussed. Second, if aid improves the conditions for
domestic investment, this effect might be relatively easy to detect. If we see consumption
and investment as jump variables, they can respond quickly to changes in aid. In contrast,
GDP is a function of state variables such as the capital stock: the relevant effects of
aid could take time to emerge, and empirical researchers have to contend with the high
degree of persistence of GDP. With these points in mind, it should be easier to establish
reliable findings for absorption than for growth. Our approach allows us to make progress
on some fronts, but not others. Although our instrument has some major advantages, it
would be difficult for us to adapt the current approach to allow for parameter
heterogeneity or non-linearities. And given the limitations of the available data, we
cannot disaggregate aid while retaining a sample large enough for the methods that we
adopt. The estimates we obtain might be best interpreted as the average effects of typical
or business-as-usual aid. The paper is therefore complementary to previous work, given its
narrower focus and the trade-offs that inevitably arise in addressing some econometric
issues and not others.3

<h>METHODS</h>
-------

As we noted earlier, when studying the effects of aid, a central problem is that aid is
not randomly assigned across countries. Even in a model that controls for country and time
fixed effects, it is likely that aid flows and outcome variables are jointly influenced by
time-varying variables that are not readily measured. To address this, we adopt a supply-
push instrument which is a weighted average of donor budgets, where the weights are fixed
over time but vary across aid recipients. One advantage of the new instrument is
especially worth a discussion. It is likely that much empirical work on aid conflates the
effects of permanent and temporary variation, just as early work on consumption conflated
the effects of permanent and transitory income (Carter, 2017). From a policy perspective,
a researcher might be more interested in determining the effects of a permanent change in
aid. One solution is to use an instrument that is correlated with the permanent component
and not with the transitory component. Since our instrument is a weighted average of donor
budgets, and individual donor budgets are persistent, it should come closer than some
precursors to identifying the effects of permanent changes in aid. In using this
instrument, we are assuming that the total aid budgets of most donors are not greatly
influenced by the time-varying conditions of many individual aid recipients. As
background, aid flows are increasingly fragmented. The number of significant donors has
increased, and most donors provide aid to a large number of countries. This is documented
in Annen and Moers (2017), Djankov et al. (2009), Easterly (2007) and Knack and Rahman
(2007), among others. Even as early as the 1970s, the US accounted for less than a quarter
of total aid flows. According to Annen and Moers, the average bilateral donor provided aid
to about 20 recipients in 1960, rising to 87 recipients by 2011. For identification, we
rely on within-donor and within-recipient fragmentation. We want to avoid correlations
between the instrument and time-varying conditions in a recipient country. If aid is
fragmented, endogeneity will arise only when the total aid budgets of multiple donors
respond simultaneously to a recipient's conditions, and to a large degree. This does not
seem especially plausible. Total aid budgets are likely to emerge from a medium-run
political process, and the hypothesized strong responses would imply greater volatility in
total aid budgets than we see in the data. If aid is not fragmented, the most serious
problem for the instrument would arise when a donor gives to a small number of recipients,
and those recipients receive most of their aid from that donor. There are few such cases
in the data. The observed fragmentation suggests that the instrument will be uncorrelated
with time-varying recipient conditions in most cases.4 To support this claim, we first
look at within-donor fragmentation. We construct Herfindahl-Hirschman (HH) indices for the
29 donors that contribute to the supply-push instrument for at least one aid recipient in
our main sample; low values correspond to aid that is distributed across many recipients,
or high fragmentation.5 Fig. 1 shows box-plots for the distribution of the HH indices
across donors, for each three-year period in our sample. If we take the box-plot for
1971–73, the upper border of the box indicates that 75% of the donors had HH indices below
about 0.30, indicating high fragmentation even in the first period. Reading across the
figure, the long-run trend is towards greater fragmentation (lower median HH indices). The
dots indicate isolated exceptions, which relate to two minor donors and a small number of
recipients. Even the exceptions are unlikely to be a problem, because these recipients
will typically receive aid from multiple sources. Since the instrument is a weighted
average of donor budgets, this should weaken the correlation between the instrument and
recipient conditions even when a subset of the donors are highly specialized. But to check
this, in the later analysis, we will consider versions of the instrument which exclude
specialized donors. The results continue to indicate strong effects of aid on total
consumption and net imports. The high degree of within-donor fragmentation supports our
approach. It suggests that the total aid budgets of these donors are unlikely to be
strongly driven by the domestic conditions of individual recipients. We next examine
within-recipient fragmentation. As indicated previously, this will promote identification
when the value of the supply-push instrument for a given recipient draws on aid from
multiple donors. This is because, even if some donors to a given recipient have total aid
budgets which are correlated with that country's domestic conditions, summing over a
larger set of donors will tend to weaken the correlation between those conditions and the
instrument. Note that, for identification, it will be fragmentation within the instrument
at the recipient level that matters, rather than within a recipient's aid. We construct HH
indices for each recipient and year, based on the contribution of each donor to that
recipient's supply-push instrument in that year. Fig. 2 shows box-plots for the
distributions of these within-instrument HH indices across recipients, drawing on the 1099
recipient-period observations in our main sample. The lines in the middle of the boxes
show the degree of fragmentation within the instrument for the median recipient: for many
recipients, the instrument is relatively fragmented, supporting identification. There are
some exceptions where recipients have HH indices close to one, and hence where the
instrument places a high weight on a single donor for that particular recipient. These are
isolated cases which are unlikely to dominate the variation, and should not threaten
identification given the within-donor fragmentation documented above.6 In summary, the
analysis suggests that a supply-push approach can be applied to the study of foreign aid.
We now turn to a different objection, which is that total aid budgets might be influenced
by disaster and emergency relief. But even broadly defined, humanitarian assistance
accounts for a small share of global aid flows: for 1995–2013, Qian (2015) finds that it
ranged between 5% and 9% of official development aid. Some humanitarian assistance is
long-term rather than emergency-related, and several of the major recipients are not in
our data set.7 Finally, since emergency relief may be funded by reallocations within
existing budgets, and disasters do not appear to have major effects on aid receipts (Qian,
2015), we do not see strong grounds to reject the supply-push approach on this basis.
Importantly, allowing for heterogeneous effects of common factors will help to ensure that
our supply-push instrument is exogenous. In contrast, conventional panel estimators with
time fixed effects assume that common factors, such as global shocks, have exactly the
same effects on all the countries in the sample.8 If the data generating process is more
complicated, identification could fail, because the instrument might be correlated with
the effects of the common factors. The combination of a supply-push instrument and a
flexible approach to common factors is new to this paper, and should achieve
identification under a wider range of circumstances than previous work. To address this,
we filter out common factors using the approach of Pesaran (2006). His paper introduced
common correlated effects (CCE) estimators for panel data. This class of estimators
proxies for the combined effects of common factors using linear combinations of the cross-
section means of the observable variables. To allow the effects of the factors to differ
across countries, the combinations are estimated from the data and vary across countries.
This is achieved by augmenting the regression with cross-section means of the dependent
variable and the explanatory variables, all with country-specific coefficients. Under a
condition on the number of linearly independent common factors, their combined effect will
be captured by the cross-section means. The method thereby addresses an important class of
omitted variables in a way that is straightforward to implement. It can accommodate
various forms of cross-section dependence, and simulations suggest that it can perform
well even in small samples and when the factors are non-stationary.9 The CCE method has
been extended to the case of instrumental variables by Harding and Lamarche (2011),
yielding a CCE IV estimator that we describe in Appendix A. This estimator is again easy
to implement. The first and second stages of 2SLS are augmented with cross-section means
of the observable variables, including the instrument, with country-specific coefficients.
This approach has costs and benefits. It builds in robustness, helping to ensure that the
instrument is exogenous. However, filtering out the common factors is parameter-intensive
and could ask a lot of the data. The key point here is that, although the benefits of CCE
IV may be offset by higher standard errors, our estimates are often precise enough to be
informative.10 Although we report the results from several methods, we give most emphasis
to CCE IV, as the estimator most likely to yield consistent estimates of the parameters of
interest. We now discuss how the paper relates to previous work. The instrument we adopt
was first used by Van de Sijpe (2010) to study aid and governance, but without allowing
for a multifactor error structure.11 Work using other supply-push instruments includes
Nunn and Qian (2014) and Werker et al. (2009). The instrument in the latter paper
interacts the world oil price with a dummy for Muslim countries, since aid to Muslim aid
recipients may be sensitive to the oil price. Werker et al. use this to study the effects
of aid on a range of outcomes, including macroeconomic ratios. Their findings tally
closely with ours. They find a significant effect of aid on consumption, where the IV
estimate is much larger; no evidence that aid leads to higher government consumption; some
evidence that aid promotes gross investment, but this is not robust; no evidence that aid
affects exports; and strong evidence that aid leads to higher imports. Although the two
papers differ in significant respects, the findings on absorption are remarkably similar.
Our approach is related to other work on aid using instrumental variables, including
Galiani et al. (2017), Jarotschkin and Kraay (2016) and Tavares (2003). The latter paper
used the distance between recipients and donors, and whether they share a common border,
language or religion, to instrument for aid. In our study, the initial shares in donor
budgets can proxy for many possible connections between donors and recipients while
remaining agnostic about their sources. Put differently, we infer connections from the
data, rather than restricting them to take specific forms. In summary, the combination of
a supply-push instrument and the CCE IV estimator is new to this paper. The approach has
several benefits. First, by using the total aid budgets of many donors to construct the
instrument, we are exploiting the fragmentation of global aid flows to lessen the risk
that the instrument is correlated with the conditions of individual aid recipients. This
will be the case even if those conditions are driven by country-level trends, for example.
Second, we use the CCE IV approach to address a remaining concern, that total donor
budgets could be influenced by common factors, such as world economic conditions, that are
correlated with conditions in aid recipients. The combination of instrument and estimator
allows us to go beyond the natural experiments studied in the literature to date, and
study the effects of broadly-defined aid from a wide range of donors.

<h>DATA</h>
----

Our models will be estimated using three-year averages over 1971–2012.12 To construct the
synthetic aid measure that we use as an instrument, we need the initial shares of aid
recipients in donor budgets. These initial shares will be based on the period 1960–1970.
Our aid variable is taken from Table 2a of the OECD Development Assistance Committee (DAC)
data tables. We follow Arndt et al. (2010) in our treatment of some missing values: they
argue that some apparently missing values in fact correspond to zeroes. In each year, we
turn missing recipient-donor-year aid to zero for combinations of recipients that receive
aid from at least one donor in that year and donors that disburse aid to at least one
recipient in that year. Aid in recipient-year format is found by keeping the entries that
list ‘All donors, total’ as a donor. Our focus is on net aid disbursements, and our final
sample comprises 88 aid recipients. The dependent variables considered will include
household consumption, government consumption, gross capital formation, imports and
exports, again relative to GDP.14 Net imports are defined as imports minus exports. In the
recipient-year data, before collapsing to three-year averages, observations for these
variables are turned to missing whenever at least one of the other components of the GDP
identity is missing. This keeps the sample consistent across the different outcomes we
consider. In our final data set, the expenditure components sum to total GDP, or very
close to GDP, for each country-period observation.15 We exclude countries with populations
fewer than 500,000 people in the first period of the sample. These steps leave us with a
panel with 1099 observations, based on 88 countries.16

<h>RESULTS</h>
-------

For each dependent variable, we report eight regressions. For reference purposes, we
report FE and pooled CCE results that do not instrument for aid. We report estimates for
static models, and models that include a lagged dependent variable.17 In each case, the
coefficient estimates indicate the effect of the aid-to-GDP ratio on the dependent
variable, also measured as a ratio. For example, in the case of net imports, a point
estimate of one implies that the ratio of net imports to GDP increases one-for-one with
the ratio of aid to GDP, corresponding to full absorption. The standard errors that we
report are heteroskedasticity-robust and clustered by country, and we make a small-sample
adjustment to take into account the large number of parameters. In experiments, we
compared adjusted standard errors to those obtained from a non-parametric block bootstrap,
given that the asymptotic distribution of pooled CCE-type estimators is non-standard
(Pesaran, 2006) and the asymptotic variance of the CCE IV estimator in Harding and
Lamarche (2011) is not known. The bootstrapped standard errors are noticeably larger than
the conventional standard errors in some cases, but our main findings obtain under either
approach to inference.18 The long-run responses of macroeconomic ratios to aid may differ
from those in the short run. The inclusion of a lagged dependent variable is one way to
capture this. Whenever the estimated model is dynamic, the long-run effect of aid is
estimated using the ratio of the short-run effect to one minus the coefficient of the
lagged dependent variable, with a standard error approximated by the delta method. Since
the long-run effect is a ratio, the estimates are likely to less precise than the
estimates of short-run effects.19 Dynamic models also have the drawback that CCE-type
estimators will be consistent under more restrictive assumptions than in the static
case.20 With this in mind, our discussion will give more emphasis to static models; the
use of three-year averages implies that, even in these models, absorption can extend over
several years. Before we turn to the results, note that the effects of instrumenting for
aid and allowing for common factors are likely to vary across the dependent variables.
Macroeconomic ratios are likely to differ in their sensitivity to particular aid-relevant
shocks, and in their sensitivity to common factors. We first study the effects of aid on
trade-related variables, starting with net imports. Recall that net imports must increase
if aid is absorbed. If the net import share rises one-for-one with the aid share, this
should assuage concerns that aid is diverted abroad (capital flight), used to accumulate
foreign exchange reserves, or spent on forms of technical assistance that do not have a
direct effect on expenditure beyond the donor country. The results are shown in Table 1.
In our IV estimates, we cannot reject the hypothesis that aid is fully absorbed
domestically. The coefficient on aid is large, significantly different from zero, and not
significantly different from unity, both in static models and in the long run derived from
dynamic models. Note the contrast with the upper row of estimates: in the absence of an
instrument, the evidence that aid is fully absorbed is weaker. We can also investigate
whether there are symptoms of aid-driven Dutch Disease. An increase in domestic
expenditure will often fall partly on non-traded goods, increasing both their relative
price and the costs facing the export sector.21 Tables 2 and 3 show the effects of aid
intensity on import and export shares respectively. The results for the import share are
similar to those for net imports, with the exception of the static model estimated by FE
IV. A strong positive effect of aid is found in the two CCE IV regressions in particular.
In contrast, we do not find a clear-cut effect of aid on the export share. In the FE IV
estimates of a static model, aid has a negative effect on the export share which is
significant at the 10% level, but this finding is not robust to alternative models and
estimators. In the dynamic FE IV estimates, and the two sets of CCE IV estimates, we
cannot reject the hypothesis that aid has no effect on the export share. This does not
rule out Dutch Disease – that finding would require zeroes estimated with greater
precision – but nor is there robust evidence that aid adversely affects exports.22 Next,
we study how aid is absorbed. Note that, since aid leads to an increase in net imports,
the GDP identity implies that the sum of household consumption, government consumption and
total investment must have also increased. The question is whether we can reliably
identify the components of GDP which respond most strongly to aid. We first look at the
effect of aid on total consumption. We define this as the sum of household and government
consumption (C + G). While household and government consumption are distinct, there are
sectors such as education and health where the distinction is somewhat artificial for
welfare purposes, given a mix of public and private provision. The results are shown in
Table 4 and suggest that aid has a large positive effect on total consumption. The
difference made by instrumental variables can be seen clearly, by comparing the upper row
of estimates with the lower row. Compared to the FE and CCE estimates, the point estimates
from IV estimators suggest larger effects of aid on total consumption. We should avoid
over-interpreting this, because the differences are not statistically significant.
Nevertheless, it is easy to see how this pattern could arise. Donors may respond to
country-specific adverse shocks by allocating countries more aid, and this form of
endogeneity will weaken the correlation between aid and total consumption. By
instrumenting aid we alleviate this source of bias, and find larger effects of aid. For
the effects of aid on household consumption, the estimates are generally similar to those
we find for total consumption, but less precise. These results are shown in Table 5. The
use of an instrument again increases the estimated effect of aid. We find much less
evidence that aid influences government consumption, as Table 6 shows. These results are
similar to those found by Werker et al. (2009, Table 2) using a different instrument. Aid
has often been characterized as primarily government-to-government transfers. Our finding
that a substantial fraction of aid is reflected in higher household consumption, but not
in higher government consumption, may be surprising. One mechanism could be lower taxes:
increased aid to governments may not be used to increase government purchases, but to
reduce taxes (Kimbrough, 1986). Alternatively, recipient governments may use aid to
finance transfers for political ends, as in Adam and O’Connell (1999), Boone (1996) and
Hodler and Raschky (2014), among others. Finally, some aid is given in ways which bypass
domestic governments, such as off-budget aid projects and support for NGOs.23 In these
cases, household consumption is where the effect of aid is most likely to be manifested in
the national accounts. Finally, we look at the effect of aid on the investment rate, in
Table 7. When aid is instrumented, the estimated long-run effect is significant at the 5%
(FE IV) or 10% (CCE IV) level. But to anticipate our later discussion, the investment
results are less robust than the consumption results. Overall, our findings are in line
with Boone (1996), who finds that aid translates mainly into consumption rather than
investment and growth. Clemens et al. (2012) present stronger evidence that aid has modest
effects on investment and growth, but note that their results are ‘not incompatible’ with
Boone's suggestion that aid is often consumed rather than invested. The 2SLS estimates of
Werker et al. (2009, Table 2) suggest that aid has stronger effects on consumption than
investment. They find no evidence that aid affects growth when using four-year averages,
which tallies with the lack of robustness of an investment effect in this paper.
Considering the magnitudes of the effects, the specification allows these to be
interpreted easily. In Table 1, for example, a one percentage point increase in aid's
share of GDP leads to a 0.772 percentage point increase in net imports as a share of GDP
(in FE IV estimates) or a 1.085 increase (in CCE IV estimates). Although these two
estimates are individually statistically significant, the difference between them may not
be significant. To investigate this, we use a bootstrap-based test described in Section
B.4 of the online appendix. For the results in Tables 1–7, we typically cannot reject the
null that the CCE IV point estimate is not significantly different from the FE IV
estimate, given their high standard errors. In choosing between them, there is a trade-off
between robustness and efficiency. The CCE IV estimator should be consistent under more
general conditions than FE IV, and hence more robust, but will usually lead to higher
standard errors. Readers may legitimately differ in which set of estimates they prefer. We
have not yet discussed the strength of our instrument. The tables report the first-stage
F-statistic as a guide, indicating the significance of the single excluded instrument.24
This approach has been widely used, but the conventional Stock and Yogo (2005) benchmarks
for first-stage F-statistics do not apply directly to panel data models. In keeping with
other papers, our application of the F-statistic in panel 2SLS is best seen as heuristic.
In most cases, and especially in the static CCE IV regressions, the first-stage robust
F-statistic is reasonably high, and the Kleibergen-Paap LM test always rejects the null of
under-identification at the 5% level.

<h>ROBUSTNESS</h>
----------

We now consider several alternative models and estimators. These will tend to increase
robustness – in the sense of reducing likely biases – at the expense of reduced
efficiency. Our main conclusions continue to find support, even when we make adjustments
to the instrument that weaken its explanatory power in the first stage. The estimates are
summarized in Table 8, where row 1 shows the main results from Tables 1–7 for ease of
comparison. Rows 2–9 then correspond to the robustness tests listed in the notes to the
table, and that we discuss below. In each row, we report the estimated effects of aid in
static and dynamic models, and the first-stage F statistics. In our main results, we
followed much of the literature and excluded countries with small populations. If we
include these countries, the instrument becomes weaker in the first stage of 2SLS: see row
2 of the table.25 A potential explanation is that, for aid recipients which account for
small and volatile shares of donor budgets, the share of a budget at an initial date may
be uninformative about that recipient's long-term exposure to changes in that budget.
Hence, we would expect our supply-push instrument to have less explanatory power for aid
to smaller countries. But despite the weakening of the instrument, the results are
qualitatively unchanged. This is also true when we exclude aid observations for colonies
prior to independence, as discussed in Section B.5 of the online appendix. Also in that
appendix, we examine whether the estimated effects of aid are driven by distinct subgroups
of countries, namely economies where natural resources play a major role, and countries
with unusually strong or weak institutions. Estimates based on subsamples continue to
suggest that aid increases consumption and net imports, while the evidence that aid
affects investment varies across samples. As before, aid appears to increase imports,
while there is no evidence of a negative effect on exports. Responses to aid may take time
to emerge, as Clemens et al. (2012) argue. In Table 8, we estimate models with lagged aid
rather than current aid (row 3) and using six-year averages of aid and the instrument (row
4).26 These point to stronger effects of aid on investment, but we interpret this
cautiously. As we discuss later, our findings on investment are more sensitive to
modelling choices than our findings on consumption and net imports. Section B.5 of the
online appendix reports on some additional variations on these robustness tests. We now
turn to potential criticisms of our instrument. Serial correlation in country-specific
conditions might undermine exogeneity (Card, 2001). Another concern is that the relevance
of the instrument could decline over time. Our IV strategy relies on the idea that shares
in donor budgets in 1960–70 are informative about exposure to later changes in total donor
budgets. If strategic or economic connections between countries evolve, the instrument may
have less explanatory power for aid in later periods. We address these concerns as
follows. Row 5 in Table 8 repeats the main analysis but excludes the first period. Row 6
uses an instrument based on initial shares calculated over the period 1960–73 and an
estimation sample that starts with 1974–76. Row 7 excludes the first period from this
sample. Section B.5 of the online appendix reports some further variations, including ones
with the initial shares calculated over 1960–76. We might expect instrument strength to
weaken when early time periods are excluded, and this is what we find. The estimated
second-stage coefficients are fairly stable, however, when dropping early time periods. In
rows 5–7, we continue to find that aid is absorbed via higher consumption and higher
imports, without much effect on exports. In experiments that drop up to three periods, the
point estimates are quite stable, but the results for total consumption become a little
less precise once we drop three periods; see Section B.5 of the online appendix. We also
note that, if serially-correlated shocks were a major problem in our static models, we
would have expected a greater contrast between static and dynamic models in Tables 1–7. It
could be argued that our instrument makes use of too many donors. By considering all DAC
donors, we have included some whose budgets could be dominated by a few recipients, which
risks endogeneity. To investigate this, row 8 in Table 8 shows results using an instrument
based only on less specialized donors, whose HH index never exceeds 0.25.27 The instrument
remains informative and the results are in line with our main findings, but yield larger
point estimates for the effects of aid on consumption and on net imports. We cannot reject
full absorption achieved through higher consumption.28 Next, we consider whether donors
have been sorting themselves across recipient countries in a way that could undermine
identification. We examine this using an approach developed by Greenstone et al. (2015).
We implement two versions of their test and, in both cases, find little evidence that
sorting has taken place. But there are some grounds for caution over the applicability of
these tests in our setting, and Section B.3 of the online appendix examines these issues
in greater detail. We also investigate the possibility of outliers. Given that we use
2SLS, outliers could arise in the first stage or the second stage. Some of our robustness
checks give rise to large first-stage F statistics, which may be a warning sign of
outliers. To address this, we use the robust instrumental variable estimator of Cohen
Freue et al. (2013), after partialling out fixed effects and cross-section means. As they
discuss, robust parameter estimates can then be used to identify multivariate outliers.
Across our dependent variables, seven countries regularly give rise to one or more
outlying country-period observations: Burundi, the Central African Republic, Chad, the
Democratic Republic of Congo, Jordan, Madagascar, and Mauritania. The results when we
exclude them are shown in Row 9 of Table 8. In line with our main findings, the instrument
retains explanatory power, and we cannot reject strong effects of aid on net imports,
household consumption and total consumption. The effects on net imports are sufficiently
strong that we cannot reject the null hypothesis of full absorption. In the dynamic model,
the increase in net imports appears to arise from higher imports rather than lower
exports. The estimated effect of aid on investment is too imprecise to draw conclusions,
and this remains the case in models (not reported) that allow for delayed effects. We now
consider an alternative estimation method. Thus far, we have emphasized estimators that
use a within transformation. For the static models, another way to eliminate country-
specific effects is to first difference the model.29 A comparison of the two approaches
should be informative about the validity of our assumptions, and help to address potential
concerns. In particular, our dependent and independent variables both contain nominal GDP
in the denominator, as does the instrument. This would be problematic if some function of
nominal GDP cannot legitimately be excluded from the models we estimate: in that case, the
instrument would be correlated with the error term. But, given the persistence of GDP,
first differencing would weaken the correlation between the instrument and the error term
in differences. Hence, we investigate the results from this approach, and compare them to
our earlier findings. The first-differenced results suggest that our earlier findings are
not spurious. Nevertheless, a sceptical observer might still be worried about a ‘false
positive’, because the variables in our regressions take the form of ratios to nominal
GDP. In principle, this could lead to an observed relationship between two ratios even
when their numerators are unrelated.30 One reason to doubt this interpretation is the
pattern of the results. We consistently find that the ratios of consumption and net
imports to GDP are increasing in aid intensity, in line with theoretical predictions,
while the effects of aid on the other ratios are weaker, again in line with theory. A
convincing story based on ‘false positives' would have to explain why spurious
correlations emerge for some ratios and not others, and why the magnitudes of the
estimated effects remain plausible. But to investigate this further, Section B.5 of the
online appendix reports on some additional analysis, including models with the dependent
variable in logarithms and the logarithm of nominal GDP included as an explanatory
variable. The results on absorption and its channels are in line with our main findings.
In summary, we have carried out a range of robustness tests. These include demanding
versions of CCE and CCE IV estimators with many additional parameters, and go beyond those
typically used in the literature. It is not surprising that the effects sometimes become
imprecise, but the point estimates are quite stable, and rarely change sign. Across a
range of models and approaches, we continue to find that aid is absorbed in line with
theoretical predictions, and with effect sizes that have plausible magnitudes. More
precise estimates are likely to require longer spans of data or the use of additional
instruments, such as those of Galiani et al. (2017) or Jarotschkin and Kraay (2016). In
the meantime, we note that our findings are consistent with Werker et al. (2009), while
adopting a new approach to identification and filtering out common factors. Moreover, in
contrast to previous studies based on distinct natural experiments, the results we present
relate to a broad concept of aid, for the full set of DAC donors.

<h>CONCLUSIONS</h>
-----------

Using cross-country data to study aid is fraught with difficulties, and yet some research
questions are hard to answer any other way. This paper has aimed to make progress on two
fronts. First, we have introduced a new instrument that can be used to identify persistent
changes in aid, and combined it with a panel time series estimator that filters out
unobserved common factors, even when their effects differ across countries. This approach
is an advance on much of the existing literature. Second, we use the instrument to
investigate the effects of aid on domestic absorption, consumption and investment, and
whether aid is associated with Dutch Disease. The evidence suggests that aid is absorbed
at least partially, and we cannot reject the hypothesis of full absorption, in which aid
increases net imports one-for-one. Absorption seems to arise mainly via increased imports,
and we find no evidence that aid lowers exports through Dutch Disease effects. We also
investigate the relationship between aid and the separate components of domestic
expenditure. Our estimates suggest that aid is absorbed primarily by increased consumption
rather than investment. Although we do sometimes find a significant effect of aid on
investment, it seems less robust than the effect on consumption. Overall, the supply-push
instrument appears to work well. For many of the dependent variables studied,
instrumenting for aid has a substantial effect on the results. The instrument is strong
enough to generate some informative findings, and as future years of data become
available, the prospects for robust and precise estimates should improve further. The
instrument could have many possible applications in the future study of aid.


<h>REFERENCES</h>
----------

  [1] Christopher S. Adam, Stephen A. O'Connell. Aid, taxation and development in Sub-Saharan Africa. doi:10.1111/1468-0343.00060
  [2] Kurt Annen, Luc Moers. Donor competition for aid impact, and aid fragmentation. doi:10.1093/wber/lhw019
  [6] Peter Boone. Politics and the effectiveness of foreign aid. doi:10.1016/0014-2921(95)00127-1
  [7] David Card. Immigrant inflows, native outflows, and the local labor market impacts of higher immigration. doi:10.1086/209979
  [8] Patrick Carter. Aid econometrics: Lessons from a stochastic growth model. doi:10.1016/j.jimonfin.2017.06.004
  [9] Michael A. Clemens, Steven Radelet, Rikhil R. Bhavnani, Samuel Bazzi. Counting Chickens when they Hatch: Timing and the Effects of Aid on Growth. doi:10.1111/j.1468-0297.2011.02482.x
  [10] Gabriela V.Cohen Freue, Hernan Ortiz-Molina, Ruben H. Zamar. A Natural Robustification of the Ordinary Instrumental Variables Estimator. doi:10.1111/biom.12043
  [11] Simeon Djankov, Jose G. Montalvo, Marta Reynal-Querol. Aid with multiple personalities. doi:10.1016/j.jce.2008.09.005
  [12] William Easterly. Are aid agencies improving?. doi:10.1111/j.1468-0327.2007.00187.x
  [13] Sebastian Galiani, Stephen Knack, Lixin Colin Xu, Ben Zou. The effect of aid on growth: evidence from a Quasi-experiment. doi:10.1007/s10887-016-9137-4
  [15] Matthew Harding, Carlos Lamarche. Least squares estimation of a panel data model with multifactor error structure and endogenous covariates. doi:10.1016/j.econlet.2011.02.001
  [16] Matthew Harding, Carlos Lamarche. Estimating and testing a quantile regression model with interactive effects. doi:10.1016/j.jeconom.2013.08.010
  [17] Roland Hodler, Paul A. Raschky. Regional favoritism. doi:10.1093/qje/qju004
  [18] Alexandra Jarotschkin, Aart Kraay. Aid, Disbursement Delays, and the Real Exchange Rate. doi:10.1057/imfer.2015.7
  [20] Frank Kleibergen, Richard Paap. Generalized reduced rank tests using the singular value decomposition. doi:10.1016/j.jeconom.2005.02.011
  [21] Stephen Knack, Aminur Rahman. Donor fragmentation and bureaucratic quality in aid recipients. doi:10.1016/j.jdeveco.2006.02.002
  [22] Nathan Nunn, Nancy Qian. US food aid and civil conflict. doi:10.1257/aer.104.6.1630
  [24] M. Hashem Pesaran. Estimation and inference in large heterogeneous panels with a multifactor error structure. doi:10.1111/j.1468-0262.2006.00692.x
  [25] Nancy Qian. Making Progress on Foreign Aid. doi:10.1146/annurev-economics-080614-115553
  [26] Vasilis Sarafidis, Tom Wansbeek. Cross-Sectional Dependence in Panel Data Analysis. doi:10.1080/07474938.2011.611458
  [28] James H. Stock, Motohiro Yogo. Testing for weak instruments in Linear Iv regression. doi:10.1017/CBO9780511614491.006
  [29] José Tavares. Does foreign aid corrupt?. doi:10.1016/S0165-1765(02)00293-8
  [31] Eric Werker, Faisal Z. Ahmed, Charles Cohen. How is foreign aid spent? Evidence from a natural experiment. doi:10.1257/mac.1.2.225
<ART>Growth and inequality in public good provision
==============================================

Authors: Simon Gächter, Friederike Mengel, Elias Tsakas, Alexander Vostroknutov
DOI: 10.1016/j.jpubeco.2017.03.002
Year: 2017  |  Pages: 1-13
ASJC codes: 2002, 2003
Keywords: Cooperation, Experiment, Free riding, Growth, Inequality, Public goods, Punishment

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

In a novel experimental design, we study public good games with dynamic interdependencies, where each agent's wealth at the end of period t serves as her endowment in t + 1. In this setting, growth and inequality arise endogenously allowing us to address new questions regarding their interplay and effect on cooperation. We find that amounts contributed are increasing over time even in the absence of punishment possibilities. Variation in wealth is substantial with the richest groups earning more than ten times what the poorest groups earn. Introducing the possibility of punishment does not increase wealth and in some cases even decreases it. In the presence of a punishment option, inequality in early periods is strongly negatively correlated with group income in later periods, highlighting negative interaction effects between endogenous inequality and punishment.

--------------------------------------------------------------------------------


<hs>  Motivation</hs>
  ~~~~~~~~~~

Social dilemmas, where collective and private interests are in conflict, abound in
economic and social life. Public good games have been used across disciplines as the
standard tool to study a wide array of social dilemma situations. These include joint
ventures (Grossman and Shapiro, 1986), R&D cooperation (Cozzi, 1999; Kamien et al., 1992),
political action funds of special interest groups or parties (Dawes et al., 1986),
multilateral foreign aid and effort provision in work teams (Ostrom, 1990; Hamilton et
al., 2003; Tirole, 1986). But also pricing or market sharing agreements by firms (Green
and Porter, 1984) as well as many economic activities in the family (Becker, 1981) can be
thought of as instances of cooperation that can be modeled with public good games. One
feature that is common to many of these examples is that there are dynamic
interdependencies: not only will the same set of people interact again, but previous
outcomes affect future endowments (both in terms of the stock of physical and social
capital). In this paper, we present a novel experimental design that captures such dynamic
interdependencies. Our design builds on what has become the workhorse model to study
public good provision in experiments (see e.g. Isaac et al. (1984), Andreoni (1995) or
Fischbacher and Gächter (2010) among many others): participants are matched in fixed
groups of four people to play the public good game for 10 or 15 periods. As in most other
public good experiments, we focus on the most challenging social dilemma situations, where
the unique subgame perfect Nash equilibrium prescribes zero contributions by all group
members, but where efficiency requires group members to contribute their entire endowment.
We also conduct experiments where each group member can punish other group members by
reducing their first stage earnings at a cost to themselves (Ostrom et al., 1992; Fehr and
Gächter, 2000; Andreoni et al., 2003). The key difference to previous research using this
“standard” design is that each participant's wealth at the end of a period constitutes
their endowment for the next period, whereas in the “standard design” endowments are
allocated exogenously and tend to be the same in each round.1 In our design, endowments
are created endogenously, which leads to dynamic interdependencies. We focus on two
important implications of introducing these interdependencies. First, if overall
contributions today are high, then there will be higher wealth in the next period
(growth). Second, heterogeneity in contributions today creates inequality in endowments in
the following period. Growth and inequality can interact with the possibility of
punishment in different ways. The threat of punishment can lead to higher growth if it
induces higher contributions, but punishment executed on the outcome path can induce a
multiplier effect which can hamper growth severely. Maybe more interestingly, punishment
can interact with inequality in non-trivial ways. In particular, rich group members can be
largely “immune” to punishment by poorer group members, if the punishment that poor group
members can afford is too small relative to the richest group member's wealth. As all
endowment can be used for punishment, rich group members, on the other hand, might be able
to punish others harshly at a relatively low cost to themselves. This asymmetry of
punishment possibilities translates wealth inequality into inequality in power to punish.
In addition, in unequal groups richer group members will typically be free-riders implying
that punishment power could be in the “wrong hands”. This raises the question of whether
punishment will be as effective in increasing contributions and group income as it has
been in settings without these dynamic interdependencies. Our main findings can be
summarized as follows. Even in the absence of punishment contribution and wealth levels
display a strictly increasing trend over time. In terms of the realized potential for
growth and the level of inequality, there is a lot of variation across groups. Individual
earnings range between 2 Euros and 241 Euros. The Gini coefficient assumes the full range
between 0 (equal wealth of all group members) and 1 (one group member appropriates the
entire wealth) in the experiment. Punishment (or the possibility thereof) does not
increase wealth. This is true in both the 10 and 15-period variations despite the fact
that people tend to contribute more in the treatment with punishment in the 10-period
variations. We find evidence for two mechanisms behind this result: (i) in groups where
inequality is high (above median) there is more anti-social than pro-social punishment,
i.e. shirkers punish contributors more than vice versa and (ii) much of this punishment
happens in early periods implying that resources are taken away exponentially.2 While the
possibility of punishment does not increase wealth and in some cases even strictly
decreases it, it also does not increase inequality on average. This is true despite the
inequality-increasing presence of anti-social punishment. Analysis of data from Herrmann
et al. (2008) shows that, in a comparable standard setting, punishment increases both
wealth and inequality. In terms of the relationship between inequality and growth, we find
that inequality in period 2 is strongly negatively correlated with wealth in period 10 in
the treatment with punishment possibilities. In particular, a 1% increase in inequality in
period 2 leads to a ≈ 0.5% decrease in wealth in period 10. Inequality and growth are
positively related across groups with below median wealth and negatively related across
groups with above median wealth. In interpreting these results, it is important to note
how the setting we introduce differs from the standard public good game described above.
There are two main differences: (i) there is no consumption until the last round in our
setting, i.e. one's entire wealth can be reinvested at the end of the period and (ii)
endowments are endogenous, i.e. determined by previous outcomes. R  +  D cooperation often
displays these features, but also the evolution of societies could be viewed under this
lens. In the standard setting, by contrast, there is full consumption, i.e. no wealth can
be reinvested and endowments are exogenous (and stationary). Volunteering, e.g. at a food
bank, seems a good example falling into this category. Other types of volunteering, such
as in natural conservation and archiving, are examples involving stationary exogenous
endowments, but no or little consumption. The case of full consumption with endogenous
endowments describes the one-shot game. Finally, note that many applications, such as
infrastructure investments, multilateral foreign aid or pricing agreements will fall
somewhere in between these extremes with some, but not full consumption and with partially
endogenous endowments.

<hs>  Literature review</hs>
  ~~~~~~~~~~~~~~~~~

To our knowledge, our experiment is the first to study public good provision with dynamic
interdependencies and endogenously arising asymmetric punishment possibilities.3 As such,
it contributes to studies of public goods with dynamic interdependencies more broadly.
These include Battaglini et al. (2016) who study the Markov perfect equilibrium dynamics
in the provision of a durable public good over time where there is consumption in each
period. They find evidence of significant under-provision relative to the interior
equilibrium. Duffy et al. (2007) studied threshold public good games with multiple
contribution rounds, where, theoretically, “completion equilibria” (with positive
contributions) do exist. They find that, as in the standard setting, contributions do
decline over time (see also Croson and Marks, 1998 among others). Noussair and Soo (2008)
and Cadigan et al. (2011) study dynamic public good settings where the current return from
the public good depends on past contributions. Other studies link public good games over
time via explicit reputation mechanisms (e.g. Milinski et al., 2002). Rockenbach and Wolff
(2017) have recently studied a setting where games are linked via endowments. They use a
non-linear exchange rate, though, which effectively eliminates the possibility of
exponential growth and contains inequality. Consequently, their results are more similar
to those obtained in the standard setting. Our results also contribute to research on the
impact of inequality on public good provision. Most existing literature has studied the
effects of exogenous income inequality. Chan et al. (1996) experimentally test a
prediction by Bergstrom et al. (1986), where public good provision increases with
inequality in the income distribution in an equilibrium with positive contributions. They
find that group behaviour conforms with the theoretical prediction. Other authors have
found that exogenous income inequality decreases contributions (van Dijk et al., 2002;
Ostrom et al., 1994) or found no effect (Chan et al., 1999). Reuben and Riedl (2013) find
that without punishment there is no effect of income inequality on contributions, while
with punishment participants contribute proportionally to their endowments, leading to
increased contributions. All these papers deal with one-shot games and exogenously imposed
inequality. Sadrieh and Verbon (2006) study exogenous inequality in the Bergstrom et al.
(1986) setting with the possibility of growth. They find that exogenous variations of
inequality are mostly neutral to growth.4 The latter result contrasts with our finding
that endogenous inequality is negatively related to growth in the presence of punishment.
One possible reason for the difference between these results is that, as discussed above,
with endogenous inequality the power to punish tends to lie “in the wrong hands” (those of
free-riders). Our paper also contributes to the literature on the standard setting of
repeated public good games surveyed in Chaudhury (2011). One insight emerging from this
literature is that societies can maintain high levels of contributions and wealth if there
is a threat of punishment to free-riders (Ostrom et al., 1992; Fehr and Gächter, 2000;
Fehr and Gächter, 2002; Andreoni et al., 2003).5 While some studies have found that
punishment can lead to lower payoffs if the horizon of the game is short (Egas and Riedl,
2008; Dreber et al., 2008), under a long horizon punishment in the standard setting has
been found to be strictly beneficial (Gächter et al., 2008). Punishment does not increase
wealth in our setting neither under a 10-period nor a 15-period horizon. We do not study
longer horizons, but since many groups in the treatment with punishment destroy (almost)
all wealth by period 10, these groups will be unable to recover even with a very long
horizon. Some studies of the standard setting investigate how an increased marginal per
capita rate of return affects contributions (Isaac and Walker, 1988; Goeree et al., 2002).
There is some relation of these studies to our setting, since the possibilities of
exponential growth provides increased incentives to contribute. Finally, the dynamic
setting we study also relates to other dynamic games studied in economics. In the common
pool resource game (CPR, Ostrom et al., 1994) players extract from a resource in each
period with the non-extracted part growing at a fixed rate. There are various differences
between this setting and our dynamic public good game (apart from the frame). One is that
whatever is contributed in our public good game is mechanically shared among all
participants. How the benefits of non-extraction are shared depend on players' strategies.
On the other hand, what is withheld in our public good game in one period can be
contributed in the next. What is extracted in the CPR game, however, cannot be reverted to
the pool in future periods. As a consequence of these various differences, both games have
different equilibria. The CPR game has an interior stationary Markov equilibrium where
players extract too much relative to the efficient benchmark (Mailath and Samuelson,
2005). By contrast, in our dynamic public good game the only equilibrium has zero
contributions in all rounds (Section 3). Herr et al. (1997) study two variations of the
CPR game, one where extraction by one player increases the cost of extraction by others in
the current period only, and one where extraction increases the costs for all future
periods. While both versions have interior equilibria, the latter type of externality
should worsen the CPR problem, i.e. lead to lower efficiency. Experimental behaviour is in
line with equilibrium benchmarks. Botelho et al. (2014) study a game that lies in between
a classic CPR and Centipede game, in that they study a CPR game which ends as soon as the
resource stock falls below a certain level. They show that increasing uncertainty about
that level increases extraction and hence the inefficiency. Battaglini et al. (2016)
discussed above can be viewed as a public good study within the CPR paradigm. This paper
is organized as follows. In Section 2, we present the experimental design. Section 3
discusses the theoretical predictions and summarizes our research questions. Section 4
contains our main results. In Section 5, we discuss the mechanisms underlying these
results. Section 6 concludes. An Online Appendix contains screenshots, experimental
instructions and the questionnaire, proofs of the theoretical predictions and several
additional results, tables and figures.

<h>EXPERIMENTAL DESIGN</h>
-------------------

In our experiment, participants play a sequence of dynamically interdependent public good
games in two main treatments: (1) treatment NOPUNISH in which participants only play the
public good game; (2) treatment PUNISH where, after each period, participants can also
subtract tokens from other members of their group at a cost. We describe these treatments
in turn.

<hs>  Treatment NOPUNISH</hs>
  ~~~~~~~~~~~~~~~~~~

Therefore, in period t + 1, the number of tokens that each participant can invest depends
on the choices of all group members in previous periods (endogenous endowments). This is
what makes our set-up different from the standard setting where the amount of tokens
before each period is fixed and the earnings from previous periods cannot be used for
investment into the public good (exogenous stationary endowments). At the end of each
period participants observe information about endowments and contributions of all group
members (Fig. A.1 in Online Appendix A).

<hs>  Additional treatments</hs>
  ~~~~~~~~~~~~~~~~~~~~~

As we outlined above, the dynamic interdependencies in this setting create two types of
effects: (i) they create the possibility for endogenous growth and (ii) they create
endogenous inequality and hence asymmetries in the power to punish others. To better
understand the impact of these two forces we ran additional treatments, where we
artificially eliminate growth (treatments NOPUNISH-NOGROWTH and PUNISH-NOGROWTH) but keep
endogenous inequality or where we artificially eliminate inequality but keep growth
(treatments NOPUNISH-NOINEQUALITY and PUNISH-NOINEQUALITY). We will discuss these
treatments in more detail in Section 5.

<hs>  Length variations</hs>
  ~~~~~~~~~~~~~~~~~

In addition to the punishment variation, we added a second treatment variation which
changes the number of repetitions of the public good game. We conducted sessions with 10
periods and sessions with 15 periods to understand how a longer horizon might affect
behaviour and hence get some insights into how participants might perceive this
environment strategically.7 Due to the (potentially) exponential increase of earnings over
time in our setting, we limited the long horizon to 15 periods.8 Participants were
informed about all these details of the design at the beginning of the experiment.

<hs>  Other details</hs>
  ~~~~~~~~~~~~~

Participants answered a sequence of questions at the end of the experiment (see Online
Appendix B). We report summary statistics on these characteristics in Tables 14 and 15 in
Online Appendix F, where analysis of the questionnaire data can be found. In all
treatments, the amount that participants received at the end of the experiment was equal
to a €2 show up fee plus the amount of tokens after the last period converted into Euros.
1 token was equal to 0.05 Euros. All experiments were run at the BEE-Lab at Maastricht
University and used z-tree (Fischbacher, 2007). Table 8 in Appendix D shows the exact
order of sessions for the main treatments. In total, 656 participants took part in our
experiment: 152 in treatment NOPUNISH (38 groups), 144 in treatment PUNISH (36 groups) and
the remainder in one of the additional treatments. Table 7 in Appendix D summarizes the
treatment structure and the number of independent observations, participants and sessions
for each treatment. Average earnings were 11.94 Euros with a minimum of 2 Euros and a
maximum of 241.65 Euros. No other sessions apart from those reported here were conducted
and there were no pilot studies.

<h>THEORETICAL BACKGROUND AND RESEARCH QUESTIONS</h>
---------------------------------------------

In this section, we briefly discuss the theoretical predictions and then present our
research questions. We focus on the standard solution concepts for dynamic games with
observable actions, i.e., Nash equilibrium (NE) and subgame perfect equilibrium (SPE)
under the standard textbook assumptions of self-interest and common knowledge of
rationality. First, observe that the games that describe our treatments are not repeated
games, as the set of available actions at each subgame depends on the moves that have been
already realized. Therefore, unlike in the standard setting, we cannot directly apply the
wide range of well-known results on finitely repeated games. Nevertheless, it turns out
that SPE leads to very similar predictions as in the standard setting. On the equilibrium
path all players contribute 0 in all periods, and moreover in the punishment treatment no
player ever punishes. The purpose of stating these results is not to argue that they will
be good predictions of behaviour, but rather to give the reader a sense of the incentive
properties of the public good game with dynamic interdependencies. In this section, we
will state the result informally. Formal statements and proofs can be found in Online
Appendix C. Consider the public good game with growth as defined above. The unique SPE of
both the game without punishment and with punishment is such that all players contribute 0
throughout the entire game (both on and off the equilibrium path). As is the case with the
standard setting, positive contributions can be sustained under different assumptions.
Particularly reputational models that invoke the existence of behavioural types such as
e.g. Kreps et al. (1982) have the potential to induce positive contributions in either
setting, but also to drive a wedge between the two settings in terms of the extent of
cooperation found. More precisely, following Kreps et al. (1982), let us assume that there
are two types of agents: (i) “standard” rational and self interested types and (ii)
conditional cooperators who start out by contributing 10 tokens and then match at each
time t the minimal contribution in their group at t − 1. We assume that all agents are of
type (i) and that each agent has a minimal doubt that other agents may be of type (ii),
i.e. conditional cooperators. More precisely we denote by μ the probability with which
agents believe that all other agents are conditional cooperators. We also denote by T the
length of the game, which in our experiment is either 10 or 15 periods. We can then state
the following result. The proof of this result can be found in Online Appendix C. Because
of the incentives provided by exponential growth, even a small doubt that some agents may
be conditional cooperators suffices to induce positive contributions on the equilibrium
path. In the standard setting, by contrast, such doubts have to be substantial (μ > 0.19)
to even get one period of positive contributions. In fact, if 0.03 < μ < 0.19 and T = 10,
then positive contributions can only be sustained in the setting with growth. For any
given μ, more periods of contributions will be observed in the setting with growth. And,
across the periods where contributions are positive, the amount contributed is constant in
the standard setting and increasing in the setting with growth (for a related result in
Centipede games, see McKelvey and Palfrey, 1992). We next summarize our research
questions. First and foremost, we are interested in whether participants contribute
positive amounts and in how much wealth is created in this game. Apart from wealth
creation, we are also interested in the amount of inequality created both within and
across groups. Of particular interest is the relation between inequality and growth. The
sign of the relation between inequality and growth of societies as well as the causal link
between the two has been at the center of a debate in macroeconomics and development
(Barro, 2000; Forbes, 2000; Persson and Tabellini, 1991). Hence, while Q1 asks whether
societies can see positive contributions and increasing wealth over time, our next
question Q2 asks how much inequality is generated in this process and how inequality
affects growth. Our setting allows us to address this question both within and across
groups. In particular, we ask whether “rich” or “poor” groups will be more unequal and how
initial inequality affects growth and hence final wealth. Last, we are interested in the
effects of punishment in our setting. Punishment has been shown to be effective in the
standard setting in securing high contributions and wealth (Gächter et al., 2008). In our
setting, however, punishment does destroy resources which could otherwise be used
productively in the following period. Punishment in the dynamic setting can have
additional adverse effects that operate via endogenously created inequality. Because
earnings are carried over across periods, free-riders in our setting will have more
resources to punish others than contributors. Hence, the possibility of punishment could
strengthen existing inequalities because it makes shirking individuals more powerful. This
in turn could undermine the effectiveness of punishment.

<h>RESULTS</h>
-------

This section comprises our main results. Section 4.1 focuses on Question 1, i.e. on how
much participants contribute and how much wealth is generated in this setting. Section 4.2
focuses on Question 2, i.e. how much inequality is endogenously created. We study the
effect of punishment (Q3) within each of these subsections. In Section 5, we discuss
additional results and possible mechanisms behind our results.

<hs>  Provision of the public good and wealth creation</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We start by discussing contributions. Panel (a) in Fig. 1 shows the average amount of
tokens participants contributed over time. Contributions are clearly non-zero and are
increasing over time in all treatments. Even without punishment participants contribute
about 10 tokens in the first period and then steadily increase this amount over time.
Contributions flatten out towards the end of the experiment and there is even a
statistically significant drop in period 15 in the long horizon game. Note that increasing
contributions over time imply that participants have increasing endowments over time.
Hence, increasing contributions do not necessarily imply that participants contribute
increasing shares of their endowments. Panel (b) in Fig. 1 shows the share of overall
endowments contributed over time in all main treatments. In NOPUNISH, participants
contribute around 55% of their endowment in period 1. This amount steadily decreases
between periods 2 and 8 and is roughly constant afterwards at a level of about 35% of
endowments. In the 15-period games, shares follow a similar pattern until period 10, then
start to decrease again afterwards. Panel (a) in Fig. 1 presents a stark contrast to
typical 10-period public good games in the standard setting, where contributions are
decreasing over time (see e.g. Figure 3 in Fehr and Gächter, 2000).9 It should be kept in
mind, though, that in the standard setting with stationary exogenous endowments, the
dynamics of contributions over time is the same irrespective of whether it is measured in
absolute terms or as a share of endowment. In Fehr and Gächter (2000), for example,
contributions equal around 50–60% of endowments in Period 1 and decrease to around 10% of
endowments by Period 10. Panel (b) in Fig. 1 shows that in our setting contributions
stabilize at a higher level (≈ 35%) in the 10-period games even if measured as share of
endowments contributed. One possible explanation is that the dynamic incentives with the
possibility of exponential growth have a similar effect to that of increasing MPCR's in
the standard setting (Isaac and Walker, 1988; Goeree et al., 2002).10 This higher level of
shares contributed seems not to be sustainable in the longer run, though. By period 15, a
similar share of endowments is contributed as in the standard setting after 10 periods
(10–20 %). Fig. 2 shows the dynamics of wealth over time. Panel (a) focuses on all groups,
panel (b) on those with above median wealth in Period 10 (“successful” groups) and panel
(c) on those with below median wealth in Period 10 (“unsuccessful” groups). Average wealth
is increasing across periods (see coefficients β1 and β4 in Tables 9 and 10 in Appendix D)
and is substantially above 80 once period 10 is reached (Table 1). Not all groups achieve
growth, however. There are several groups where wealth does not rise (substantially) above
80. Figs. E.1–E.2 in Online Appendix E illustrate wealth (and Gini coefficients) over time
in different matching groups. Amounts contributed are positive and increasing over time
even without punishment. Wealth is growing over time, but there is large variation across
groups with the richest group earning more than 10 times more than the poorest after 10
periods and more than 55 times more after 15 periods.

     <hss>Effects of punishment on contributions and wealth</hss>

        We next consider the effect of punishment on contributions and wealth. Absolute
        contributions end up higher in PUNISH compared to NOPUNISH (Panel (a) in Fig. 1),
        but they start to differ only from period 7 onwards in the 10-period games and in
        the 15-period games they are higher only in the very last period. In terms of
        shares contributed (Panel (b) of Fig. 1), in PUNISH, contributions are roughly
        constant across all periods at a level of about 60%, though there is a slight
        decrease towards the end of the 15 period games. This is above the share at which
        groups stabilize in treatments without punishment. However, groups in PUNISH are
        also poorer. Median wealth is higher in NOPUNISH compared to PUNISH (Table 1) and
        the difference in mean ranks is statistically significant in the 10-period games
        according to a one-sided ranksum test (p < 0.0001 for all periods; p = 0.0928 for
        t = 10 data only). To assess the statistical significance of differences in means,
        we run OLS regressions where we regress wealth on a treatment dummy for PUNISH
        (Table 2). These regressions show that differences in means are only significant
        for below median groups in the 10-period games which earn on average 213 tokens
        less in PUNISH compared to NOPUNISH. Several of these groups, in fact, end up with
        zero income in PUNISH. In the 15-period games, differences are statistically
        significant across all groups with mean wealth in period 15 being about 790 tokens
        lower in PUNISH compared to NOPUNISH. The fact that punishment seems more harmful
        the longer the horizon stands in contrast to results obtained in the standard
        setting by e.g. Gächter et al. (2008). Columns (1) and (2) of Table 9 in Appendix
        D assess differences in time trends using a linear (column (1)) and square (column
        (2)) polynomial in period. While wealth is increasing in both treatments (β1,β1 +
        β3), the linear trend in column (1) is no different across treatments (β3). The
        square polynomial does reveal differences in time trends, though. While wealth is
        initially increasing at a lower rate in PUNISH (β3), it increases at a faster rate
        in later period (β5). Fig. 2 illustrates these results. It shows that wealth is
        lower in PUNISH compared to NOPUNISH across all periods except for the last three
        periods in the 10-period games. Overall, these results indicate that the threat of
        punishment is not needed to sustain high contributions in public good games with
        growth and does not increase wealth. Instead, the dynamic evolution of the public
        good drives contributions and wealth. This is in stark contrast to what we know
        from other social dilemma games, where punishment has been shown to be successful
        in both raising contributions (in Fehr and Gächter’s (2000) study on the standard
        setting by around 600%) as well as wealth in later periods (in Fehr and Gächter’s
        (2000) study from period 4 onwards (Result 8 in Fehr and Gächter, 2000). In
        Section 5, we discuss in more detail why punishment is less effective in our
        setting. There we also analyze data from an experiment by Herrmann et al. (2008)
        conducted in the standard setting and show that in this case punishment leads to
        unambiguously higher wealth. The possibility of punishment does not increase
        wealth. In the long horizon games (15 periods), average wealth is even lower in
        PUNISH compared to NOPUNISH.

<hs>  Inequality</hs>
  ~~~~~~~~~~

In this subsection, we focus on the amount of inequality created endogenously in our
setting. As measure of inequality we use the Gini coefficient as defined in Deaton (1997).
The smallest possible value the Gini coefficient takes is zero (if all four group members
own one fourth of the wealth) and the largest possible value it takes is one (if one group
member holds the entire wealth). Table 1 shows some summary statistics regarding the Gini
coefficient. The period 10 Gini coefficient ranges between 0 and 0.43 in NOPUNISH with a
median of 0.22 and assumes the full range between 0 and 1 in PUNISH with a median of 0.03.
The period 15 Gini coefficient ranges between 0.03 and 0.49 in NOPUNISH and between 0 and
0.67 in PUNISH. Fig. 3 illustrates the dynamics of the Gini coefficient over time. The
figure shows that in NOPUNISH inequality is sharply increasing from the initial value of
zero and then increases more slowly between periods 2 and 10 to reach a level of ≈ 0.2 in
period 10 (β2 and β4 in column (2) of Tables 11 and 12 in Appendix D). Interestingly,
these patterns almost perfectly mimic the trends in inequality identified in a recent
paper by Nishi et al. (2015) (see their Fig. 2) who study the effect of visibility of
wealth (and inequality) in a cooperation game played on a network. A longer horizon seems
to lead to slower growth in inequality, but by period 15 Gini coefficients are not
statistically different from those reached in period 10 of the shorter horizon games.
Panel (b) shows groups with above median wealth, which display lower levels of inequality
than those with below median wealth illustrated in Panel (c) (ranksum test p < 0.001 all
periods, p = 0.1096 period 10, p > 0.1 period 15). Mean Gini coefficients are increasing
over time reaching ≈ 0.2 in the last period. There is substantial variation in Gini
coefficients across groups, particularly in PUNISH where the Gini assumes the full range
between 0 and 1 in the 10-period games.

     <hss>Effects of punishment on inequality</hss>

        We next study the effect of punishment on inequality. Mean Gini coefficients are
        similar across treatments and there are no statistically significant differences
        in mean Gini coefficients between NOPUNISH and PUNISH in period 10 or 15,
        respectively (see Table 4). By contrast, analysis conducted with data from a
        standard public good game in Section 5.4 shows that in this setting punishment
        leads to more inequality. In fact, in our case the median Gini coefficient tends
        to be even higher in NOPUNISH compared to PUNISH (Table 3). The difference in mean
        ranks is statistically significant (one-sided ranksum test p = 0.0395) only in the
        10-period games. There is also more variation in PUNISH (one-sided variance ratio
        test on period 10 data only, p < 0.0001; period 15 data: p < 0.0001) where the
        Gini coefficient assumes the full range between 0 and 1 in the 10-period games and
        between 0 and 0.67 in the 15-period games. Fig. 3 illustrates these results as
        well as differences in time trends. Across all groups (Panel (a)) the dynamics of
        inequality seem similar across treatments with somewhat more volatility in PUNISH.
        Columns (1)–(2) of Table 11 in Appendix D show that there are few statistically
        significant differences in these time trends. The dynamics of inequality over time
        seem also quite similar in above median groups, where the difference is mostly one
        of means (Panel (b)). In below median groups, however, time trends are quite
        different across treatments (Panel (c)). In NOPUNISH, inequality is steadily
        increasing over time at a slow rate, while in PUNISH, the Gini coefficient seems
        to follow a different pattern. After increasing initially, it decreases sharply
        around periods 4–7 and then starts to increase again. One possible interpretation
        is that this pattern reflects cycles of reciprocal punishment. Depending on who
        punishes (shirkers or high contributors) inequality increases or decreases. We
        discuss differences in punishment behaviour between below and above median groups
        in more detail in Section 5.3. Mean inequality (Gini) is not statistically
        different in PUNISH compared to NOPUNISH in period 10 (15). There is more across-
        group variation in inequality in PUNISH.

<h>DISCUSSION AND ADDITIONAL RESULTS</h>
---------------------------------

In this section, we discuss some of the potential mechanisms underlying our main results.
Section 5.1 discusses results on the relationship between growth and inequality. In
Section 5.2, we will try to tease apart the effect of exponential growth opportunities
from the effect of endogenously created inequality. In Section 5.3, we provide some
additional results on punishment, which should help us get a deeper understanding of why
punishment is less effective here than in the standard setting. Finally, in Section 5.4,
we use data from experiments conducted by Herrmann et al. (2008) to study wealth and
inequality in the standard setting.

<hs>  The relation between growth and inequality</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We study the relationship between growth and inequality across and within groups starting
with across-group inequality. In NOPUNISH, the two variables are essentially uncorrelated.
The Spearman correlation coefficient is  −0.1840 in above median groups and  −0.0630 in
below median groups, neither of which is statistically different from zero. In PUNISH, by
contrast, there is a substantial and statistically significant relationship between these
two variables. In above median groups the correlation is negative (Spearman correlation
coefficient ρ = −0.6091**): higher wealth comes with lower inequality. In fact, most
groups that achieve very high levels of wealth in period 10, have a Gini coefficient of
almost zero. For below median groups, the correlation is positive (ρ = 0.4683*): higher
wealth comes with higher inequality. As a consequence inequality is highest in groups with
intermediate levels of wealth in PUNISH. Fig. D.1 in Appendix D illustrates the
correlation between period 10 wealth and Gini coefficients for both treatments. The same
patterns hold in the 15-period games, but, possibly due to lower power, there is no
statistical significance. These differences between above and below median groups appear
already as early as in the second period of the game. For NOPUNISH, both successful (above
median wealth in period 10) and unsuccessful (below median wealth in period 10) groups
have a Gini coefficient of 0.13 on average in period 2. In the 15-period games, these
numbers are 0.13 and 0.14, respectively. In PUNISH, on the other hand, there are
substantial differences. Groups that are eventually successful have a Gini coefficient of
about 0.11 in period 2 (0.10 in the 15-period games), while unsuccessful groups have a
Gini coefficient of 0.27 (0.25 in 15-period games), more than twice as high. Hence,
successful and unsuccessful groups already differ after the first round of the public good
game. This observation motivates us to study the extent of path dependency within groups.
Table 5 presents evidence in this respect. It shows the correlation between wealth in
period 10 (period 15) and the wealth or the Gini coefficient in previous periods. Path
dependence is evident. Early period wealth is strongly correlated with late period wealth.
The Spearman correlation coefficient between periods 2 and 10 income is 0.48*** in
NOPUNISH and even 0.82*** in PUNISH. Maybe more interestingly, also early period
inequality is highly detrimental to final wealth, but only in PUNISH. The correlation
between inequality in period 2 and wealth in period 10 is  −0.47***, which is substantial.
In NOPUNISH, by contrast, early period inequality (in periods 2–4) is not negatively
correlated with wealth. In this treatment the negative correlation appears only from
period 5 onwards. The fact that there is no negative correlation between periods 7, 8, and
9 inequalities and period 10 wealth in PUNISH is due to the fact that by then, several
groups have zero wealth and inequality. Dropping these groups restores the negative
correlation. Comparing 15 period wealth and early period inequality (bottom panel of Table
5) shows similar patterns. One question about these findings is whether they just reflect
a stable distribution of “contribution types” or whether there is something more
fundamental to it in the sense that the same people are more likely to end up with a much
lower wealth if initial inequality is high. The fact that the negative correlation between
early period inequality and wealth is only observed in PUNISH, suggests that this is not
just a mechanical effect of having different distributions of “contribution types” across
groups. Additional support for this view can be derived from our post-experimental
questionnaire. Table 16 in Online Appendix F shows the average amount in Euros that
participants decide to donate to Medics without Borders at the end of the experiment. We
find that participants from above median groups do not contribute more on average than
those from groups with below median wealth. This is despite the fact that participants
from groups with above median wealth earn 178 tokens on average in period 10 (189 in
treatment PUNISH), while those from groups with below median wealth earn only 56 tokens
(23 tokens) on average in period 10. This suggests that participants in groups with above
median wealth are not per se more altruistic than others. We also elicited 14 other
personality characteristics as well as a measure of risk aversion in the questionnaire.
Tables 17–18 in Online Appendix F show that none of them is able to explain the variation
in wealth or inequality that we observe. 1. In PUNISH, wealth and Gini coefficient are
positively correlated for poor groups (below median wealth) and negatively correlated for
rich groups (above median wealth) in the 10-period games. These correlations are weak and
not statistically different from zero in NOPUNISH. 2. (a) Early period wealth is
positively correlated with eventual wealth in all treatments. (b) Early period inequality
is negatively correlated with final wealth only in PUNISH. Taken together, both the
findings on across- as well as within-group correlation point to a detrimental role of
inequality if there are punishment possibilities. One of the reasons, hence, why
punishment is not as effective in this setting seems to be that people react strongly to
inequality. The findings are also indicative as to why we observe such substantial
variation across groups both in terms of wealth and inequality. Groups in which initial
behaviour leads to high inequality seem to get locked into a path of punishment and
counter-punishment (interpreted as experimental equivalents of conflict) that eventually
leads to a destruction of all wealth. We will see more evidence of such behaviour in
Section 5.3. In fact, there is a strand of literature, where economic historians point out
the importance of institutional lock in with institutions broadly understood as both
formal constraints, such as rules and laws and informal constraints, such as norms of
behaviour, conventions and codes of conduct (North, 1994). Our study provides an example
of how a society (group) can get locked into dysfunctional behavioural norms. Before we
conclude this section, let us point to potential links to other literatures. The sign of
the relation between inequality and growth as well as the causal link between the two has
been at the center of a debate in macroeconomics and development (see e.g. Barro, 2000;
Forbes, 2000; Persson and Tabellini, 1991, among many others). Most of these authors find
either a negative relation or no significant relation at all. In our context, the relation
depends on the wealth of the group. For very poor groups in our data, inequality and
wealth are positively related, while they are negatively related for richer groups. This
is reminiscent of the famous Kuznets curve (Kuznets, 1955) which claims an inverse
U-shaped relationship between growth and inequality. The connection between our setting
and the fate of countries is too loose to draw any conclusions. Our results suggest,
however, that there may be interesting links, between the level of social capital
(cooperation, trust), the level of inequality and the level of growth of societies.11

<hs>  Eliminating inequality and growth possibilities</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

This means that each participant's endowment ranges between 0 and 80 in each round and the
sum of endowments in a group equals 80 in each period. This 10 period game hence, can be
viewed as a public good game played in period 10, where the endowment each participant has
is determined by the game played in periods 1–9. The unique SPNE is zero contributions in
each period as in our main treatments. Note that this structure, while derived from our
treatment NOPUNISH via a single change creates a situation where everyone contributing no
longer Pareto dominates nobody contributing in periods 1–9. Consequently, participants may
have different motives for contributing in these treatments compared to our main
treatments and the results should be interpreted with this in mind. We do the analogous
normalization for the punishment version (PUNISH-NOGROWTH). We had 116 participants (29
groups) in treatment NOPUNISH-NOGROWTH and 92 participants (23 groups) in treatment
PUNISH-NOGROWTH. Table 13 (column (1)) in Appendix D shows the results of regression where
we regress normalized contributions on treatment dummies. The baseline is NOPUNISH. To
ensure a fair comparison, we also normalize contributions in NOPUNISH and PUNISH.
Normalized contributions in these treatments are computed by multiplying the share of
actual endowment contributed with normalized endowments. Maybe unsurprisingly, given the
absence of even social incentives to contribute across periods 1–9 of the games without
growth, contributions are substantially lower and close to zero. The second column in
Table 13 (Appendix D) shows that inequality leads to lower contributions in both the
treatments with and without punishment. Eliminating inequality increases mean
contributions by 26 tokens without punishment and by 42 tokens with punishment.
Furthermore, if inequality is eliminated then mean contributions are ≈ 24 tokens higher
with punishment (PUNISH-NOINEQUALITY) than without (NOPUNISH-NOINEQUALITY), a difference
that is statistically significant (χ2 < 0.001). It seems that endogenous inequality in
endowments with the associated inequality in the power to punish undermines the
effectiveness of punishment. Since we exogenously remove inequality in the treatments
discussed here, the results from this section support a causal interpretation of the
effect of inequality on wealth.

<hs>  Anatomy of punishment</hs>
  ~~~~~~~~~~~~~~~~~~~~~

Both Sections 5.1 and 5.2 have pointed to a negative role of inequality for contributions
and wealth particularly in treatment PUNISH. To understand why this is the case it is
helpful to study punishment patterns more closely. We first compare above and below median
groups in treatment PUNISH to understand which patterns of punishment lead to low wealth
in this treatment and are hence crucial for the ineffectiveness of punishment in this
setting. Fig. 4 reveals an interesting pattern in this regard. It shows the amounts of
tokens participants use to punish over time. In groups with above median wealth, the
absolute amounts used to punish tend to remain stable or increase over time (OLS
coefficient: 1.402* (10 periods); 0.098 (15 periods)),13 while they tend to decrease in
below median groups (OLS coefficient:  −0.830*** (10 periods);  −0.332*** (15 periods)).
Particularly striking is the fact that, in terms of amounts, the major difference between
above and below median groups seems to lie in how much they punish in the first two
periods of the game (two-sided ranksum test p < 0.0001). In successful groups, there is
also an interesting peak in punishment one period before the game ends. This suggests that
some participants may tolerate some degrees of free-riding while they wait to punish
others harshly at the end of the game. This seems intuitive because of the detrimental
effect that punishment can have on growth. While in below median groups, most punishment
happens in the beginning of the game, above median groups punish at the end.14 We next ask
under which conditions punishment is “pro-social” and when it is “anti-social”. Herrmann
et al. (2008) have found that anti-social punishment strongly undermines successful
cooperation in the standard setting, whereas pro-social punishment fosters cooperation.
Punishment by player i is pro-social if i punishes a player who has contributed a lower
share of his endowment to the public good than i herself. Punishment by player i is anti-
social if i punishes a player who has contributed a higher share of his endowment to the
public good than i herself. Table 6 shows that there is more pro-social punishment than
anti-social punishment (one-sided ranksum test, p < 0.0001). Anti-social punishment is
higher if inequality is high (pro-social: Spearman ρ = 0.0155 (ρ = 0.1231***, 15 period
games); anti-social: ρ = 0.0777** (ρ = 0.1515***, 15 period games)). Anti-social
punishment is not significantly related to wealth (ρ = −0.0109; ρ = 0.1184 in 15 period
games), but there is more pro-social punishment in high-wealth compared to low-wealth
groups (ρ = 0.1371***; ρ = 0.2302*** in 15 period games).

<hs>  Wealth and inequality in the standard setting</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Before we conclude, we have a brief look at data from the standard setting. We focus on
wealth and inequality, as those are not commonly reported measures in the standard
setting. In particular, we use data from experiments that Herrmann et al. (2008) conducted
in Bonn. Bonn and Maastricht are at only 120 km driving distance and a large share of
students at both Universities comes from the lower middle Rhine and upper lower Rhine area
(between Koblenz and Duesseldorf) in Germany. This should make subject pools approximately
comparable. Just as us, Herrmann et al. (2008) conducted 10 period games with an endowment
of 20 tokens (in their case exogenously given each period). They also conducted NOPUNISH
and PUNISH treatments with the 3:1 technology that we employ. The return on contributing
in the one-shot game was 0.375 in our experiments and at 0.4 slightly higher in Herrmann
et al. (2008). Fig. 5 shows wealth and inequality (Gini coefficient) over time in Herrmann
et al. ’s ( 2008 ) experiments. We computed wealth by adding income of all group members
in each period and subtracting 80 in each period 2,…,10. If all group members contribute
zero in each period (and do not punish) wealth thus computed is 80 in each period, just as
in our setting. If all group members contribute their full endowment in each period (and
do not punish) maximal wealth in period 10 is 3075 in our setting and 1280 in Herrmann et
al. (2008). Fig. 5 shows that both wealth and inequality are substantially higher under
the punishment condition in Herrmann et al. ’s ( 2008 ) experiments (t-test period 10
sample means: p < 0.01). The effect of punishment, hence, differs from what we observe in
the dynamic setting, where punishment, if at all, decreases wealth and inequality. Note
also, that we do not observe the cyclical pattern in inequality identified in the PUNISH
treatments in our setting. In summary, Section 5.1 demonstrates a negative correlation
between early period inequality and wealth in period 10 in treatment PUNISH. The negative
impact of inequality on contributions and wealth is confirmed with some caveats in Section
5.2 where we find that artificially removing inequality increases contributions and wealth
both with and without punishment, but with a particularly strong effect in the punishment
treatments. Section 5.3 provides some insights into why inequality is so detrimental in
the punishment condition. There are two main effects: (i) in groups where inequality is
high (above median) there is more anti-social than pro-social punishment, implying that
shirkers punish contributors more than vice versa and (ii) much of this punishment happens
in early periods in unsuccessful groups implying that resources are taken away
exponentially. All these channels contribute to the negative impact of punishment
possibilities on wealth creation in the dynamic setting. The absence of inequality in
endowments in the standard setting seems to make wealth inequality less salient. This can
potentially explain why punishment does not trigger the adverse affects identified in the
dynamic setting in the standard setting (Section 5.4).

<h>CONCLUSIONS</h>
-----------

We studied public good games with dynamic interdependencies, where each agent's wealth at
the end of a period serves as her endowment in the following period. We found that
contributions are increasing over time even in the absence of punishment possibilities.
The possibility of punishment does not increase wealth. These results suggest that in
settings with a strong dynamic component societies achieve cooperation via the incentives
provided by the dynamic evolution of the public good and not so much via the threat of
punishment. Across groups, inequality in early periods is strongly negatively correlated
with wealth in later periods. These results show that people are able to establish
persistent cooperation in a setting that shares one key feature with many real-life
interactions: past behaviour matters for future endowments. They also point to the limits
of punishment in securing high contributions and wealth. The results highlight the
importance of incorporating the dynamic aspects, present in many real-life interactions,
explicitly in experimental designs. In this paper we have done so within the context of
cooperation and public good provision. We should emphasize, though, that we view this
design as complementary to the standard design where contributions occur from stationary
exogenous budgets. Both settings have natural applications outside the lab. Public goods
are often created by providing effort, as e.g. in the case of volunteering. In these
cases, clearly, endowments cannot easily increase over time. In many other settings, such
as those discussed in the Introduction 1, provision of public goods creates wealth from
which future public goods can be provided. The evolution of societies might be viewed
through this lens. We have seen that the two settings can yield quite different
conclusions. In the standard setting with stationary budgets and full consumption,
punishment has shown to be very effective at raising contributions and wealth (in the
medium run). In the dynamic setting studied here, the effectiveness of punishment seems
much more limited. It is not successful in raising wealth in the 10-period games and is
even detrimental to wealth in the games with longer horizon. Future research should aim at
getting a deeper understanding of the mechanisms behind these differences and adapt this
setting to other contexts where dynamic interdependencies are likely to play an important
role. Studying intermediate settings, with some but not full consumption and only
partially endogenous endowments should also be of interest for future research.


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<ART>Human capital and international portfolio diversification: A reappraisal
========================================================================

Authors: Lorenzo Bretscher, Christian Julliard, Carlo Rosa
DOI: 10.1016/j.jinteco.2015.12.007
Year: 2016  |  Pages: S78-S96
ASJC codes: 2002, 2003
Keywords: Hedging human capital, Home country bias, Incomplete markets, International diversification puzzle, Non-traded human capital, Optimal portfolio choice

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We study the implications of human capital hedging for international portfolio choice. First, we document that, at the household level, the degree of home country bias in equity holdings is increasing in the labor income to financial wealth ratio. Second, we show that a heterogeneous agent model in which households face short selling constraints and labor income risk, calibrated to match both micro and macro labor income and asset returns data, can both rationalize this finding and generate a large aggregate home country bias in portfolio holdings. Third, we find that the empirical evidence supporting the belief that the human capital hedging motive should skew domestic portfolios toward foreign assets, is driven by an econometric misspecification rejected by the data.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

International finance theory emphasizes the effectiveness of global portfolio
diversification strategies for cash-flow stabilization and consumption risk sharing.2
However, the empirical evidence on international portfolio holdings favors a widespread
lack of diversification across countries and a systematic bias toward home country assets
(see, e.g., Coeurdacier and Rey, 2013 for a recent survey). This discrepancy between
theoretical predictions and observed portfolio constitutes the international
diversification puzzle (see, e.g., French and Poterba, 1991). Moreover, albeit the degree
of home bias has been reducing during the last few decades, it remains a first order
characteristic of portfolio holdings.3 In the major industrialized countries, roughly two-
thirds of gross domestic product goes to labor and only one-third to capital. Thus, human
wealth likely constitutes about two-thirds of total wealth, suggesting that if investors
attempt to hedge against adverse fluctuations in returns to human capital when making
financial investment decisions, the mere size of human capital in total wealth makes its
potential impact on portfolio holdings self-evident. Based on this observation, several
contributions have argued that when the role of human capital is explicitly taken into
account, the observed home country bias in portfolio holdings becomes harder to
rationalize. The argument, originally formalized by Brainard and Tobin (1992) with a
stylized example, works as follows: if returns to human capital are more correlated with
the domestic stock market than with the foreign ones, labor income risk can be more
effectively hedged with foreign assets than with domestic ones, and equilibrium portfolio
holdings should be skewed toward foreign securities.4 As emphasized by Cole (1988), “this
result is disturbing, given the apparent lack of international diversification that we
observe.” However, as first suggested in Bottazzi et al. (1996), human capital hedging
could also lead toward home country bias in portfolio holdings. For instance, the
correlation between domestic return on physical and human capital can be lowered by
idiosyncratic shocks that lead to a redistribution of total income between capital and
labor. In the presence of these rent shifting shocks, foreign assets become a less
attractive hedge for labor income risk—especially if total factor productivity shocks are
highly correlated internationally. If the size of the rent shifting shocks is large
enough, a situation in which domestic assets are the best hedge against human capital risk
arises, therefore leading to home country bias in portfolio holdings. In this paper, we
ask whether the human capital hedging motive is likely to have a sizeable effect on
optimal portfolio choice, and what its implications are for the international
diversification puzzle. Moreover, we propose a rationalization of the home country bias,
based on a setting of endogenous portfolio formation and incomplete markets, that not only
can rationalize aggregate portfolio holdings, but also the variable degree of home country
bias in households' portfolios. In particular, Fig. 1 depicts a novel (to the best of our
knowledge) finding about households' equity home bias.5 Panel (a) depicts the (locally
weighted regression of the) share of foreign assets in U.S. household portfolios as a
function of the household financial wealth to labor income ratio. Since (labor income)
flows and stocks (of human capital) are cointegrated, Panel (a) shows that there is a
systematic relationship between household specific home country bias and the household
specific financial to human capital ratio: the degree of home country bias monotonically
decreases as the human capital component of household total wealth becomes smaller
relative to the household financial wealth. That is, in micro data, when the human capital
hedging motive is more prominent relative to the financial wealth hedging motive,
household portfolios show a higher degree of home country bias. Moreover, panel (b) of
Fig. 1, that depicts the (locally weighted regression of the) number of stocks in U.S.
household portfolios as a function of the household financial wealth to labor income
ratio, shows that when the households' human capital wealth is relative larger than the
financial wealth, the household portfolio will tend to be overall less diversified. Our
paper provides a rationalization of both of these findings, as well as of the aggregate
home country bias, and also shows that the canonical intuition that human capital should
skew portfolio holdings toward foreign assets, and the related supporting empirical
evidence, are both very fragile. In particular, we offer two main contributions. First,
using novel estimates of the correlations of human capital and stock market return
innovations, we calibrate an incomplete market model in which agents face both
idiosyncratic and aggregate labor income risk, as well as borrowing constraints.6 The
model is also calibrated to match the microeconomic (following Gourinchas and Parker,
2002) characteristics of the U.S. labor income and track the distribution of the asset
wealth to labor income ratios observed in the Panel Study of Income Dynamics (PSID). The
main findings of this calibration exercise are that a) investors that enter the stock
market with a low level of liquid (i.e. financial) wealth to labor income ratio will
initially specialize in domestic assets and, b) only as the level of asset wealth to labor
income ratio increases do agents start diversifying their portfolios internationally by
progressively adding different assets to their holdings, c) as a consequence, the
aggregate portfolio of U.S. investors shows a large degree of home bias. What drives these
results? Households face large human capital risk, but this is mostly of the idiosyncratic
type—hence underestimated in a homogeneous agent setting. Moreover, in the presence of
liquidity constraints, agents cannot borrow to construct an optimally diversified
portfolio. Therefore, when their level of liquid wealth to labor income ratio is
sufficiently high and they enter the stock market, agents try to minimize the overall
wealth risk, investing first in the asset that has the lowest degree of correlation with
labor income innovations—and, as discussed below, this assets is, in the data, the
domestic stock. Only when the ratio of liquid wealth to labor income is sufficiently high,
and the labor income risk hedging motive becomes less important relative to the financial
risk hedging one, do agents start investing in foreign assets and diversifying their
portfolios internationally. Since the distribution of liquid wealth to labor income is (in
the data as in the model) concentrated in the region of low liquid wealth to labor income
ratios, the resulting aggregate portfolio is heavily skewed toward domestic assets. Note
that, in the absence of market frictions and idiosyncratic risk, the estimated and
calibrated correlations of labor income and returns innovations, being very small, would
have almost no effect on the optimal portfolios. Moreover, since in our model the
aggregate home country bias depends on both the household optimal investment policy
functions and the aggregate distribution of liquid wealth to labor income, a trend of
increasing concentration of financial wealth (as documented by Piketty, 2014), and/or a
negative trend in the labor share of income (as documented by Karabarbounis and Neiman,
2013), would both generate a negative trend in the degree of home country bias as found by
Coeurdacier and Rey (2013).7 Since the pattern of correlation of innovations to labor
income and returns plays an important role in our calibration, our second contribution
hinges upon the identification of a common misspecification that has affected the previous
empirical literature, and the provision of novel estimates that are not affected by this
issue. In particular, we show that the seminal empirical result of Baxter and Jermann
(1997) that, in the presence of a human capital hedging motive, investors should short
sell the domestic capital stock—implying that “the international diversification puzzle is
worse than you think”—is largely due to an econometric misspecification rejected by the
data: the assumption that there are neither cross-country shocks to human and physical
capital payoffs, nor common long run trends. We show that, once this restriction is
relaxed, the effective degree of technological and economic integration becomes evident,
therefore reducing the opportunities to hedge human capital risk by investing in foreign
assets. Moreover, we also show that there is substantial uncertainty attached to the
estimation of aggregate physical capital returns via the canonical Campbell and Shiller
(1988) cum vector autoregression (VAR) approach. This feature of the data provides a
rationalization for the apparently contradictory empirical evidence on the correlation
between returns to human and physical capital found in the previous literature (that
typically has not reported confidence bands for the estimated correlations): Lustig and
Nieuwerburgh (2008) find a strong negative correlation between domestic returns to
physical and human capital in U.S. data; Bottazzi et al. (1996) find such a correlation to
be negative in all the countries they consider but the United States, where they find it
to be strongly positive; Baxter and Jermann (1997) find this correlation to be positive
and very close to one for all the countries they consider (United States, United Kingdom,
Germany, and Japan). Nevertheless, we find that by restricting the set of assets available
to hedge human capital to include only publicly traded stocks—what we consider as the
relevant case for most households—much sharper estimates can be obtained, and these are
the estimates used in our calibration exercise discussed above. We find that in this case
human capital hedging can help explain the home country bias in portfolio holdings—since
domestic returns to human capital tend to be systematically more correlated with foreign
stock markets—but, we show, given the small magnitudes of the estimated correlation, the
effect is quantitatively very small in a frictionless complete market setting.8
Nevertheless, as discussed above, this same small correlations have very large aggregate
effects in an incomplete market settings in which agents face both idiosyncratic and
aggregate labor income risk. Note that, overall, our result that domestic capital markets
constitute a good hedge for domestic human capital risk are in line with the findings of a
large empirical literature. Palacios-Huerta (2001) finds that if human capital is included
in the definition of wealth, gains from international financial diversification for a
mean-variance investor appear to be smaller than previously reported. Lustig and
Nieuwerburgh (2008) find that innovations in current and future human wealth returns are
negatively correlated with innovations in current and future domestic financial asset
returns. Abowd (1989) finds a large and negative correlation between unexpected union wage
changes and unexpected changes in the stock value of the firm. Davis and Willen (2000),
using data from the PSID to construct synthetic cohorts, find that the correlation between
domestic labor income shocks and returns on the S&P 500 is substantially negative for some
categories.9 Moreover, they find that for six out of the eight sex-education groups
considered in their study, a long position on the worker's own industry represents a good
hedge for labor income risk. The empirical works of Gali (1999), Rotemberg (2003), and
Francis and Ramey (2004) also document a negative correlation between labor hours and
productivity conditioning on productivity shocks. Coeurdacier and Rey (2013), conditioning
on exchange rate movements, find that wages and dividends growth rates comove negatively
for all the countries they consider (also Coeurdacier et al., 2013 ; Heathcote and Perri,
2013 provide similar empirical evidence). Theoretically, we show that a situation in which
labor income innovations are more correlated with the domestic payout to capital than the
foreign ones—as we find in the data—is likely to arise once the degree of international
economic integration observed in the data is properly taken into account. In particular,
we show that very small redistributive shocks (shocks with a variance that is equal to as
little as 6%–11% of the output variance), are enough to make the domestic equity market
the best hedge for human capital risk. The analysis presented in this paper is part of the
literature that has attempted to explain home bias as a hedge against non-tradable
risks.10 Moreover, the potential rationalization of the international diversification
puzzle we document in this paper should be interpreted as complementary, rather than
alternative, to the ones based on transaction and information frictions (e.g. Van
Nieuwerburgh and Veldkamp, 2009; Bhamra et al., 2014), nominal stickiness (e.g., Engel and
Matsumoto, 2009), non-traded goods (e.g., Heathcote and Perri, 2013) and more broadly the
role of real exchange rate fluctuations (e.g., Coeurdacier, 2009; Kollmann, 2006; Baxter
et al., 1998). The remainder of the paper is organized as follows. Section 2 presents a
calibrated model of human capital risk hedging in which households face both idiosyncratic
and aggregate labor income risk, as well as liquidity constraints. Section 3 presents the
empirical approach undertaken to measure factor returns and rationalizes the difference in
results between our findings and the previous empirical literature. The final section
outlines the conclusions of the paper, while a detailed data description, as well as
additional results and robustness checks, are reported in the Appendix.

<h>PORTFOLIO CHOICE WITH HETEROGENEOUS HUMAN CAPITAL RISK AND LIQUIDITY CONSTRAINTS</h>
--------------------------------------------------------------------------------

In this section we rely on numerical methods to compute the equilibrium outcome of a model
that directly takes into account that i) most of the human capital risk faced by
households is idiosyncratic in nature, and ii) households' optimal portfolio choice is
influenced by liquidity constraints. The simple incomplete markets model presented below
is a generalization of Heaton and Lucas (1997) to a multiple asset context and of
Michaelides (2003), and builds upon the household income process estimated by Gourinchas
and Parker (2002).

<hs>  Model setup and calibration</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~

Given the assumptions on the primitives and the calibrated values, these conditions hold
and there exists a unique set of optimal policies satisfying the Euler equations. To avoid
the curse of dimensionality of numerical solutions and, most importantly, in order to have
sufficiently long time series for the estimation of the variance covariance matrix of
labor income innovations and asset returns using the unrestricted VAR approach presented
in Section 3 below we focus on four countries: the United States (as domestic country),
the United Kingdom, Japan, and Germany. As we show in Section 3 below not restricting the
VAR representation to have country specific block exogeneity is both required by the data,
and needed in order to uncover the true degree of hedging potential via international
diversification.12 Since the U.S. domestic risky asset has enjoyed both the lowest
variance and the highest Sharpe ratio compared to the other countries considered, and this
pushes the optimal portfolio to be skewed toward the domestic stock, we calibrate all the
countries as having the same mean return and Sharpe ratio as the United States. A summary
of the calibrated preference and labor income process parameters are reported in Table 1.
The crucial element in calibrating the model is the covariance structure of asset returns
and innovations to the aggregate labor income process. We measure capital returns using
broad stock market indexes and calibrate their covariance using the time series sample
analogous. The calibration of the covariance structure of aggregate labor income shocks
and stock market returns is summarized by the correlations reported in the first four
columns of Table 2. These are based on the estimation approach discussed extensively in
Section 3 below where we show that the (different) estimates obtained in the previous
literature are due to misspecification. The crucial element in Table 2 is that the
correlation between U.S. labor income innovations (fourth column) with the domestic stock
market is marginally smaller than the ones with foreign stock markets returns (expressed
in dollar terms). Note that these correlations are all small in magnitude and, as shown in
Table A5, would have a very small effect on the optimal portfolio choice in a complete
markets setting. As a benchmark, the last column of Table 2 reports the implied optimal
portfolio shares of the domestic portfolio absent any human capital hedging motive and
shows that, according to the estimated covariance structure of returns, the share of U.S.
assets in the U.S. domestic portfolio would be about 25% in the absence of aggregate labor
income risk.

<hs>  Investors' optimal policy rules and portfolio choice</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Having calibrated the model, we can estimate the optimal policy function by standard
numerical dynamic programming techniques (see, e.g., Carroll, 1992 ; Haliassos and
Michaelides, 2002) to compute the optimal consumption and asset holding rules. Since the
time t optimal policy rules depend both on the normalized cash-on-hand and on the last
labor income shock (εt −1), we numerically integrate out this last variable to have policy
rules as a function of the cash-on-hand only,13 obtaining the investment rules
{b(x),sd(x),si(x)}. Moreover, from Eq. (5) we can obtain the optimal consumption rule c
(x). Optimal policy rules are plotted, as a function of normalized cash-on-hand, in Fig.
2. Not surprisingly, the optimal consumption policy rule has the same shape as in the
buffer stock saving literature, with consumption being equal to cash-on-hand (no saving
region) until a target level of cash-on-hand is reached and saving starts taking place.
Once the saving region is reached, the consumers specialize in stocks, disregarding bonds.
This result, well known in the literature, was originally obtained by Heaton and Lucas
(1997) in a domestic portfolio choice settings, and it reflects the implication of the
large equity premium for the optimal portfolio choice. More interestingly, when the
consumer enters the saving region, she initially invests only in the domestic stocks and
only gradually diversifies her portfolio internationally as the level of cash-on-hand
increases. This happens for three reasons. First, only a small buffer stock saving is
needed for the agent to protect herself from future labor income shocks. Second, when
entering the saving region, the agent prefers to invest in the assets that have the
smallest correlation with labor income shocks, in order not to increase her overall level
of risk correlated with income. This is due to the fact that, when entering the investment
region, almost the entirety of the agent's wealth is in the form of human capital. Hence,
for relatively low levels of cash-on-hand, the human capital hedging motive dominates the
portfolio diversification motive. As a consequence, the order in which the agents start
investing in the different stock markets closely match the inverse rank of the
correlations between labor income innovations and asset returns. Third, only for very high
levels of liquid wealth to labor income ratio (high x) does the financial portfolio
diversification motive become more important than the labor income hedging one, and the
agent starts diversifying fully her portfolio. This is due to the fact that, as x
increases, so does the non-human capital component of the household wealth, therefore
reducing the human capital hedging motive. Comparing this result with the empirical
distribution of cash-on-hand in the PSID data set, less than 1% percent of the population
should be investing positive amounts in all four of the assets considered. Moreover, given
the positive correlation between normalized cash-on-hand and asset wealth observed in the
data, the results imply that only the richest households will be diversifying their
portfolio internationally, coherently with the empirical evidence on households' portfolio
holdings at the micro level (see, e.g., Jappelli et al., 2001). Using the estimated policy
functions, we can compute the optimal portfolio shares as a function of cash-on-hand.
These optimal shares are reported in Fig. 3. The figure shows a large bias toward domestic
assets in all the relevant ranges of standardized cash on hand, implying that more than
99% of the households should have an asset portfolio strongly biased toward domestic
assets. Compared with the optimal share of domestic assets in the market portfolios
without aggregate labor income risk (25% in Table 2), this represents a home country bias
of individual portfolios that ranges from 75% to 19%. Even investors in the top 1% of the
distribution of cash-on-hand observed in the data would have, on average, more than 50% of
their asset wealth invested in domestic stocks. Interestingly, this large home bias is
generated by extremely small differences in the correlations between labor income shocks
and market returns across countries, and a very small aggregate labor income risk
component. Moreover, as shown by counterfactual calibration results,14 this effect is
mostly driven by the ordering, rather than the magnitudes, of the correlations between
labor income innovations and stock market returns. This implies that small shocks that
lower the correlation between aggregate labor income innovations and market returns at the
country level can generate, in the presence of short selling constraints and buffer-stock
saving behavior, a very large degree of domestic bias in portfolio holdings.

<hs>  Implications for the aggregate portfolio</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

This subsection derives the implications of the optimal investment rules, obtained in the
previous subsection, for the aggregate portfolio of U.S. investors. The standardized cash-
on-hand in Eq. (6) follows a renewal process and can be shown to have an associated
invariant distribution,15 and this can be used to compute the implied aggregate portfolio
of U.S. investors. Moreover, given the estimated policy functions, the aggregate portfolio
can also be computed using the observed empirical distribution of cash-on-hand. Second, we
can alternatively draw random initial levels of x to reproduce the initial heterogeneity
in wealth among agents, and then simulate dynamically the evolution of normalized cash-on-
hand over time, generating what we refer to as the dynamic distribution of the model. We
perform both procedures since the first one requires fixing ex-ante the relevant range of
x while the second one instead determines the relevant range autonomously, therefore
providing a robustness check of the construction of the model ergodic distribution. Fig. 4
reports the distribution of normalized cash-on-hand implied by the model and the observed
distribution of normalized cash-on-hand in the PSID data.16 The model seems to reproduce
fairly well the location of the mode and the shape of the right tail of the empirical
distribution, but the model distribution is much less concentrated than the data around
the boundary between the saving and the no saving zone, implying a higher participation
rate in the market than what is observed in the PSID data, probably due to the absence of
stock market entry costs in the setup of the model. With these distributions at hand, we
can compute the implied aggregate portfolio shares of U.S. investors. The first column of
Table 3 reports, as a benchmark comparison, the CAPM market portfolio implied by the
calibrated covariance structure of returns in the absence of labor income risk. The
implied aggregate portfolio shares of the model are reported in the second column. There
is a dramatic effect of labor income risk on the aggregate portfolio with about 95% of the
market portfolio invested in domestic assets. Moreover, the relative investments in
foreign stocks are strongly affected, with a reduction of the portfolio shares in
individual foreign stocks moving from the 18%–36% range to the 0%–4% range. Since agents
with different levels of normalized cash-on-hand are likely to have different amounts of
wealth invested in the stock market, the simple computation of the aggregate portfolio
reported in column two of Table 3 could be a poor approximation of the aggregate
portfolio. To address this issue, the third column of Table 3 weights the model
distribution by the contribution to the aggregate portfolio of agents having different
levels of cash-on-hand. This weighting of the distribution also corrects for the fact that
the model implies a higher degree of market participation than what is observed in the
data. The weights are constructed from the PSID data and are proportional to the total
stock market holdings of households belonging to each category of normalized cash-on-hand.
This weighting somehow reduces the degree of home bias relative to column two, but still
delivers a portfolio share of domestic stocks of about 75%, implying that hedging human
capital increases the portfolio share of domestic stocks by as much as 50% and decreases
the portfolio shares of German, Japanese, and U.K. stocks by, respectively, 15%, 19% and
17%. The last two columns of Table 3 show that our main result also holds if we compute
the aggregate portfolios using the empirical (again, for PSID data), rather than the model
implied, distribution of cash-on-hand, with (column five) and without (column four)
weighting. The aggregate portfolio shares implied by the empirical distribution are, in
both cases, quite similar to the ones obtained by weighting the model distribution (column
three) and carry the same message: the human capital hedging motive generates a very large
home country bias, with an increase of the portfolio shares of domestic assets between 36%
and 50%. But what is the key mechanism delivering a large home bias generated by the model
in Table 3? The driving force of our results is that small differences in the correlation
of aggregate labor income innovations and market returns, in the presence of short-selling
constraints, lead to a gradual international diversification of investors' portfolio as
their level of normalized cash-on-hand increases. In the presence of liquidity
constraints, agents cannot borrow to construct an optimally diversified portfolio.
Therefore, when their level of liquid wealth to labor income ratio is sufficiently high
and they enter the stock market, agents try to minimize the overall wealth risk, investing
first in the assets that have the lower degree of correlation with labor income. Only when
the ratio of liquid wealth to labor income is sufficiently high, and the labor income risk
hedging motive becomes less important relative to the financial risk hedging motive, do
agents start diversifying their portfolios. Note that this is exactly the pattern found in
the Survey of Consumer Finance data, and reported in Fig. 1. Since the distribution of
liquid wealth to labor income is—in the data as in the model—concentrated in the region of
low liquid wealth to labor income ratios, the resulting aggregate portfolio is heavily
skewed toward the asset with the lowest correlation with aggregate labor income shocks.
Therefore, the human capital hedging motive, once market frictions and idiosyncratic labor
income risk are taken into account, is likely to explain a large fraction of the home
country bias in several countries. The above results imply that domestic shocks that lead
to a redistribution of total income between capital and labor, therefore lowering the
correlation between return on physical and human capital, are likely to skew portfolio
holdings toward domestic assets. In Appendix A.3 we show that very small redistributive
shocks (shocks with a variance that is equal to as little as 6%–11% of the output
variance), can indeed make labor income innovation more correlated with foreign, rather
than domestic, market returns innovation. Many kinds of shocks are expected to have an
effect on the income distribution that can rationalize the correlations observed in the
data and used in our calibration. Common examples are political business cycles and
changes in the bargaining power of unions relative to firms. Among others, the works of
Bertola (1993) and Alesina and Rodrik (1994) suggest that changes in the time patterns of
capital and labor returns may be the endogenous outcome of majority voting. Santa-Clara
and Valkanov (2003) find that in the United States the average excess returns on the stock
market are significantly higher under Democratic than Republican presidents. Moreover, if
nominal wages and prices have different degrees of stickiness, demand and technological
shocks will have redistributive effects on real payoffs to labor and capital. Supportive
evidence for redistributive shocks can be found in the empirical literature: Abowd (1989),
in a study on wage bargaining in the United States, finds a large and negative correlation
between unexpected union wage changes and unexpected changes in the stock value of the
firm; Bottazzi et al. (1996), using a VAR approach that imposes block exogeneity across
countries (and hence, as discussed in the next sections, is likely to overestimate the
benefits of international portfolio diversification), find that the correlations of
returns to human capital with domestic market returns is smaller than the one with foreign
market returns in 7 out of 10 countries in their study (with an average difference of
0.19); Lustig and Nieuwerburgh (2008)17 uncover a negative correlation between innovations
to human and physical capital returns in the United States; Gali (1999), Rotemberg (2003),
and Francis and Ramey (2009) document a negative correlation between labor hours and
productivity conditioning on productivity shock. Note also that the above results have
been obtained without considering the exchange rate risk connected with the investment in
foreign assets. In the sample period considered, the lower bound on the estimated standard
deviation of exchange rates in the three countries considered is about one-third of the
standard deviation of market returns. Moreover, the exchange rates show a weakly positive
correlation with the stock market of the foreign country and seem to be uncorrelated with
the U.S. stock market and with labor income innovations.18 Therefore, adding exchange rate
risk to the model would reduce the Sharpe ratio of foreign assets, making foreign
investment less attractive and increasing the degree of home bias.

<hs>  Relaxing the borrowing constraints</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As a robustness check of the above results we now relax the short-selling constraint
restriction. Relaxing this restriction reduces the buffer stock saving need, since short-
selling increases the households' ability of smoothing wealth shocks over time via
borrowing at the risk free rate (i.e. shorting the risk free asset). In particular, we
relax the constraint by allowing the household to borrow (i.e. short-sell) up to a
constant fraction of its annual (permanent component of) labor income. Table 4 computes
the aggregate domestic portfolio as in Table 3 but considering a different level of
households' borrowing capacity in each of its panels: in Panel A through D, respectively,
short-selling is constrained to be no more than 20%, 50%, 100% and 200% of annual labor
income. The table shows that the effect of relaxing the borrowing constraints is non-
monotonic. Moderate and intermediate borrowing ability actually increases the degree of
home country bias generated by the human capital hedging motive. On the other hand,
allowing for extremely large borrowing reduces the degree of home country bias generated
by the model. This non-monotonicity is quite intuitive. With moderate borrowing ability,
when the household is sufficiently wealthy to invest in the financial market, it uses its
borrowing capacity to leverage and hedge further the human capital risk by skewing
holdings toward the domestic stock. As a consequence, the model in this case generates
even more home country bias in portfolio holdings than in the baseline specification with
no short-selling (reported in Table 3). When instead the household can borrow large
amounts, given the large equity premia, borrowing at the risk free rate to invest in
stocks is an attractive investment (for a power utility investor). Since the expected
utility from the financial investment is maximised with a well diversified portfolio, a
tension between human capital hedging and financial wealth diversification arises. As a
consequence, when the household can borrow large amounts relative to the size of its human
capital, the financial wealth diversification motive reduces the degree of home country
bias in portfolio holdings. Nevertheless, even with the unrealistically high borrowing
capacity considered in panels C and D, the model generates very large home country bias.19
This is due to the fact that the human capital of the household has a value that is a
large multiple of its annual labor income (formally, the present discounted value of all
future labor income), while the borrowing capacity, in realistic calibrations, is only a
relatively small fraction (or a small multiple in panels C and D) of the current labor
income.

<h>MEASURING FACTOR RETURNS</h>
------------------------

To assess the role of human capital in determining optimal portfolio choice, and in
particular to estimate the correlation between human and physical capital innovations, one
needs to study the time series properties of the returns to human and physical capital.
This task is complicated by the fact that neither the market value nor the returns to
human and (total) physical capital are observable. Nevertheless, total payouts to both
factors of production are directly observable from national accounting figures. Moreover,
total payouts to the labor force and capital holders can be thought of as the aggregate
dividends flows on the unobserved stocks of human and physical capitals. We can therefore
use the Campbell and Shiller (1988) methodology to infer the time series properties of
unobserved aggregate returns from the observed growth rates of dividends on human and
physical capital. To make the above approach operational, we need to construct empirical
proxies of the expected values in Eq. (9). We perform this task following Campbell and
Shiller (1988) and use linear projections generated by a reduced form VAR in a similar
fashion as in the seminal work of Baxter and Jermann (1997). There are two important
implicit restrictions in Eq. (12). First, the first matrix on the right-hand side of the
equation has all the off-diagonal matrices restricted to be zero, i.e., each country is
assumed to be block exogenous with respect to the other countries: the first differences
of log labor and log capital income of each country are not supposed to Granger-cause the
first differences of log labor and log capital income in other countries. Second, the
cointegration structure in the second term on the right-hand side of Eq. (12) rules out
cross-country cointegrations between incomes of the factors of production—that is, it
rules out international common trends (e.g., it rules out that capital income in different
countries follows the same long-run stochastic trend). Our empirical analysis in the next
subsection relaxes both of these restrictions and considers a more general class of VAR
models for labor and capital incomes that allow for short- and long-run comovements across
countries.

<hs>  Empirical evidence: a reappraisal</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We estimate Eqs. (9) and (12), as well as alternative VAR specifications, using annual
data on labor income and capital income from OECD National Accounts for Germany, Japan,
the United Kingdom, and the United States over the period 1960–2012. Our measure of labor
income is total employee compensation. This is a less than ideal measure in that it is
likely to contain components that are not purely compensation to labor (e.g. the wage bill
received by an entrepreneur might contain capital compensation components), and
consequently the literature has developed more accurate measures of compensation to labor
(see, e.g., Gopinath et al., 2015). Nevertheless, using more accurate measures of wage
compensation would require focusing on much shorter time series: depending on the
approach, we would lose between 39 and 75 per cent of the time series dimension, and in
such a reduced sample it would not be feasible to test for block exogeneity since the
number of parameters to be estimated would be too large relative to the number of
observations. Similarly, we are constrained to use a relatively small cross-section of
countries (that, nevertheless, account more than half of the world equity market
capitalization at the end of our sample, and more than 90% of the world capitalization at
the beginning of the sample), since expanding to more countries would not only
substantially increase the number of parameters to be estimated in each equation of the
VAR system,22 but also shorten the available time series since the countries we consider
are exactly the ones with the longest available history of wage bill data. This data
limitation, nevertheless, has the advantage of making our results directly comparable to
the previous literature and, in particular, to Baxter and Jermann (1997) since we use
exactly the same set of countries and definition of the wage bill. Our baseline measure of
capital income is GDP at factor cost minus employee compensation. A detailed description
of the dataset is given in Appendix A.1.

     <hss>Model selection</hss>

        The restrictions imposed in Eq. (12) by Baxter and Jermann (1997) can be formally
        tested against more general specifications that allow for international
        comovements in the payoffs to the factor of production. We start by assessing
        whether the block exogeneity assumption is supported by the data. Table 5 reports
        frequentist tests of the null hypothesis of block exogeneity in Eq. (12). Both
        restricted and unrestricted specifications are estimated with only one lag (as in
        Baxter and Jermann, 1997), and we maintain the hypothesis of cointegration
        relationships only within the countries as in Eq. (12). As stressed by the
        p-values reported under the test statistics, the null hypothesis of block
        exogeneity is rejected at any standard confidence level. That is, the data suggest
        that there exist statistically significant cross-country links between the
        compensations of the factors of production. Table 6 reports the logs of the Bayes
        factor and the posterior probabilities defined by Eqs. (14) and (15) for a large
        set of models, under the assumption of flat priors and equal prior probability for
        each model. The models considered are as follows: i) vector error correction
        models—with (row 1) and without (row 2) block exogeneity restrictions—in which, as
        in Baxter and Jermann (1997), the only cointegrations allowed are within country
        and the fixed cointegration vector has the form [1, −1]; ii) VARs in levels with
        the block exogeneity restriction which relax the assumption of having a
        cointegration vector of the form [1, −1] (rows 3 and 4); iii) VARs in first
        differences (with, row 5, and without, row 6, block exogeneity) which rule out any
        form of cointegration among variables; and iv) unrestricted VARs in levels (rows 7
        and 8) that allow for international comovements and arbitrary cross-countries—as
        well as within country—cointegration relationships. The maximum number of lags
        considered for each specification is naturally restricted by the sample size at
        hand, but nevertheless corresponds to the one chosen by Akaike and Bayesian
        information criteria. The econometric model considered in row 1 of Table 6
        corresponds to the original Baxter and Jermann (1997) specification. The second
        row shows that relaxing the block exogeneity assumption leads to a dramatic
        increase in the log Bayes factor (log BFi). This increase is so large that if the
        models in the first two rows were the only ones considered, we would assign a
        posterior probability of about one to the specification that—unlike Baxter and
        Jermann—allows for international comovements among variables. That is, Bayesian
        testing confirms the strong rejection of the block exogeneity assumptions
        delivered by frequentist testing presented in Table 5. The models considered in
        the third and fourth rows maintain the block exogeneity assumption but, by
        considering VARs in levels, do not restrict the within country cointegration
        vector to take the form [ −1,1]. The Bayes factors of these specifications are of
        similar magnitude to the one in the first row, but much smaller than the one in
        the second row, providing additional evidence of a strong rejection of the block
        exogeneity assumption. The VARs in first differences with and without block
        exogeneity in rows 5 and 6 are relevant because they impose the restriction of no
        cointegration among variables. Since the Bayes factor in row 5 is smaller than the
        one in row 1, and the one in row 6 is smaller than the one in row 2, the data
        provide supporting evidence for within country cointegration in the payoffs to
        physical and human capital. Nevertheless, in Appendix A.4, we report a detailed
        frequentist analysis of within country cointegration and find mixed evidence in
        support of this hypothesis: the [ −1,1] cointegration vector is always rejected
        except for Japan, while relaxing this parameter restriction the results vary from
        country to country and with the lag length considered. Finally, the specification
        in rows 7 and 8 of Table 6 are unrestricted VARs in levels with one and two lags,
        respectively. These specifications allow for arbitrary cointegration within and,
        most importantly, across countries—that is, the variables are allowed to show both
        short- and long-run systematic comovements across countries. The specification
        with two lags (which can be mapped into a VECM) in row 8 delivers a Bayes factor
        that is substantially higher compared to all the other models considered. This
        large Bayes factor maps into a posterior probability (POj in the second column of
        Table 6) that is numerically indistinguishable from 1. That is, the data provide
        strong evidence of both short- and long-run cross-country comovements in the
        payoffs to human and physical capital, implying that the econometric model of
        Baxter and Jermann (1997)—that rules out both of these channels—is misspecified.
        To test the robustness of the above results, we use numerical integration of Eq.
        (13) (we used an importance sampling approach based on the asymptotic Normal-
        inverse-Wishart shape of the posterior to perform this task) to get alternative
        estimates of the Bayes factors and posterior probabilities in Table 6. We also
        experimented with non-flat priors over the parameters space. In both cases, the
        results are in line with the ones in Table 6. Overall, the results of this
        subsection imply that to accurately measure returns to human and physical capital,
        and their implications for international portfolio diversification, we should use
        an econometric specification that, differently from the ones used in the previous
        literature, allows for both short- and long-run international comovements in the
        payoffs to production factors.

     <hss>The correlation of human and physical capital returns</hss>

        In order to estimate factor returns using Eq. (9) and the selected VAR model, we
        calibrate the parameters ρ to 0.957 for both capital and labor income. This
        corresponds to assuming that the mean dividend–price ratio of labor income and
        capital income are identical and equal to 4.5% as in Baxter and Jermann (1997).
        Moreover, note that finiteness of the empirical estimate of the right-hand side of
        Eq. (9) is guaranteed if ρ times the largest eigenvalue of the companion matrix of
        the selected VAR model is within the unit circle. This condition is satisfied by
        our choice of ρ. Table 7 reports the correlations between returns on capital and
        labor computed using Eq. (9) and the estimations of expected Δd’s by the VAR in
        levels specification with two lags. The correlations are both qualitatively and
        quantitatively different from the ones derived by Baxter and Jermann (1997). The
        within countries correlations seem to be somewhat lower compared to Baxter and
        Jermann (1997): their estimates cover the range [0.78, 0.99], while our estimates
        have a maximum of 0.96 and a minimum of 0.67 in Japan.24 The between countries
        correlations appear to be higher compared to Baxter and Jermann (1997): their
        maximum correlation between returns on capital is 0.43 (U.S.–Germany), the maximum
        correlation between returns on labor is 0.35 (U.S.–Germany), the maximum
        correlation between domestic labor returns and foreign capital returns is 0.40
        (Germany–U.S.). In our estimation, the between countries correlations for both rL
        and rK are much higher (with the exception of Japan, where the correlations
        between labor returns and foreign returns on both capital and labor are generally
        lower). The correlations between returns on capital, for example, cover the range
        [0.73, 0.98]. Moreover, for all countries but Japan, the correlations between
        domestic returns on labor and foreign returns on capital are similar to the
        correlation between domestic returns on labor and capital. These results suggest
        the presence of productivity shocks effective at the international levels. The
        factor returns that we obtain by applying Eq. (9) are generated regressors (Oxley
        and McAleer, 1993). To account for this, we compute the standard errors of the
        corresponding correlation matrix using a bootstrap approach to statistical
        inference (see, e.g., Efron and Tibshirani, 1993). More specifically, we apply a
        sampling-with-replacement raw residuals bootstrap scheme with 10,000 repetitions.
        Interestingly, as shown in Table 7, we find large empirical confidence intervals.
        For Japan, the confidence intervals indicate that the correlation between factor
        returns may be either positive or negative. In other words, we document the
        existence of substantial statistical uncertainty on measuring returns to the
        aggregate capital stock. The differences between our point estimates and the
        results of Baxter and Jermann (1997) are mostly driven by the relaxation of the
        block exogeneity assumption, which turns out to be strongly rejected by the data.
        Baxter and Jermann (1997) fit a model where they restrict the countries not to be
        economically and technologically integrated. As an outcome, the level of between
        countries correlation is underestimated and the within country correlation is
        overestimated (i.e., the countries appear not to be integrated). Once this
        restriction is removed, the effective degree of technological and economic
        integration becomes evident. This high degree of economic integration implies
        fewer opportunities to hedge the human capital risk investing in foreign
        marketable assets. For comparability, in Table A5 of Appendix A.6, we replicate
        the optimal portfolio implied by the complete spanning approach of Baxter and
        Jermann (1997). That is, we replicate the authors' main result, but after
        correcting their VAR misspecification (i.e. we use the VAR specification in Row
        (8) of Table 6). Raw point estimates indicate that the authors' original claim,
        i.e. that the home country bias is generally worsened by the human capital hedging
        motive, is not generally supported by the data: the table shows that, for some
        countries, we obtain exactly the opposite effect. Moreover, confidence intervals
        show that there is substantial uncertainty about optimal portfolios constructed
        with this approach, and that human capital hedging can potentially generate large
        home country bias.25

     <hss>The correlation of human capital and stock market returns</hss>

        Estimating returns to physical capital using the approach in Eq. (9) might be
        inappropriate for evaluating international portfolio diversification, since i)
        only a subset of the claims to capital compensation in a country are tradable
        internationally with relatively little frictions—i.e., the ones of publicly traded
        companies, and ii) due to tax advantages, the compensation to capital elicited
        from national accounts tends to include de facto components of human capital
        compensation (e.g., for family owned and individual firms). As a consequence, a
        more appropriate measure of the correlation between human and physical capital
        compensations can be constructed replacing the VAR based estimates of returns to
        capital with the returns on broad stock market indices. In this subsection, we
        restrict the set of assets available to hedge human capital to include only
        publicly traded stocks, since we consider this as being the relevant case for most
        households. The innovations to human capital compensation are estimated as in the
        previous subsections. Table 8 reports the correlations between the returns to
        human capital and returns to the stock market. Since the correlation between U.S.
        human capital innovations and stock returns plays a key role in the model
        calibration presented in Section 2, for the United States we use three different
        stock indices: the Fama and French (1992) benchmark market return,26 the S&P 500
        index, and the Dow Jones Industrial index. Overall, the table suggests that
        domestic returns to human capital are in general more correlated with foreign
        stock markets: for all countries considered, the asset with the highest
        correlation with human capital returns is always a foreign asset. Moreover, in the
        United States in particular, returns to human capital have the lowest correlation
        with the domestic, rather than the foreign, stock market index. However, the
        estimated correlations tend to be quantitatively small (this is consistent with
        the findings of Fama and Schwert (1977)), and the uncertainty attached to the
        estimation of human capital delivers large confidence intervals (in particular,
        only one of the estimated correlation coefficients is different from zero at the
        95% confidence level). Nevertheless, as shown in Table A4 of Appendix A.5, despite
        the large confidence intervals, the pattern of lower correlation of human capital
        with domestic, rather than foreign, returns, is quite robust to alternative
        construction of the data. The small correlations in the tables have two important
        implications. First, when focusing on tradable claims to physical capital, the
        assumption of complete spanning for human capital return used in the previous
        literature seems to be unsupported by the data. Second, if one were to use a value
        weighted approach for the determination of optimal portfolios as in Baxter and
        Jermann (1997), the effect of human capital hedging would be very small, but it
        would tend to skew holdings in favor of domestic assets, as shown in Table A5 in
        Appendix A.6. For robustness, we have also estimated the correlations in Table 8
        using two subsamples of equal length (pre and post 1987). The correlations in the
        two subsample are not statistically different from the full sample ones, albeit
        smaller in the second subsample. More importantly, the subsample estimates
        highlight the same pattern as in Table 8: labor income innovations tend to be more
        correlated with foreign stock markets than domestic ones. 27 Nevertheless, as we
        have shown in Section 2 above in the presence of borrowing constraints and both
        aggregate and idiosyncratic human capital risk, even the above small correlations
        can have a very large impact on optimal portfolio decisions.

<h>CONCLUSION</h>
----------

This paper shows that human capital risk can help rationalize the home country bias in
equity holdings at both the aggregate and household levels. First, we show that the
theoretical intuition that short positions in domestic physical assets are a good hedge
for human capital risk is a very fragile one, as very small redistributive shocks—e.g.,
with a variance of a mere 6% of GDP variance—are enough to reverse this intuition.
Moreover, we find that the presence of this type of shocks is supported by the data.
Second, we show that the commonly used approach of estimating country-specific VARs to
compute returns to human and physical capital is rejected by the data and delivers
mechanically biased estimates of the hedging benefits of shorting the domestic capital.
Most importantly, we show that this misspecification largely drives the findings of Baxter
and Jermann (1997)—i.e., the result that the home bias puzzle is unequivocally worse than
we think once we consider human capital risk, is the outcome of an econometric
misspecification strongly rejected by the data. Moreover, we show that when returns to
physical capital are measured using broad stock market indexes, human capital return
innovations tend to be more correlated with foreign rather than domestic stocks.
Nevertheless, these correlations are small and, consequently, in a frictionless complete
market setting, have very little impact on optimal portfolios. Fourth, calibrating a
buffer stock saving model consistent with both micro and macro labor income dynamics—hence
taking into account that individual labor income uncertainty is substantially larger than
the aggregate one— as well as stock market data, we show that a large home country bias
arises as an equilibrium result. This is due to the fact that household labor income risk
is about one order of magnitude larger than aggregate labor income risk and, in the
presence of liquidity constraints, optimal hedging becomes heavily skewed toward the asset
whose innovations have the lowest correlation with the labor income innovations—the
domestic asset. Moreover, our heterogenous agents model implies that, at the household
level, the degree of home country bias should increase, and portfolio diversification
decrease, in the labor income to financial wealth ratio—and these are exactly the novel
empirical stylized facts that we uncover in the 1992–2013 U.S. Survey of Consumer Finances
data.


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----------

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<ART>Income inequality and the labour market in Britain and the US
=============================================================

Authors: Richard Blundell, Robert Joyce, Agnes Norris Keiller, James P. Ziliak
DOI: 10.1016/j.jpubeco.2018.04.001
Year: 2018  |  Pages: 48-62
ASJC codes: 2002, 2003
Keywords: Earnings, Family income, Inequality

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We study household income inequality in both Great Britain and the United States and the interplay between labour market earnings and the tax system. While both Britain and the US have witnessed secular increases in 90/10 male earnings inequality over the last three decades, this measure of inequality in net family income has declined in Britain while it has risen in the US. To better understand these comparisons, we examine the interaction between labour market earnings in the family, assortative mating, the tax and welfare-benefit system and household income inequality. We find that both countries have witnessed sizeable changes in employment which have primarily occurred on the extensive margin in the US and on the intensive margin in Britain. Increases in the generosity of the welfare system in Britain played a key role in equalizing net income growth across the wage distribution, whereas the relatively weak safety net available to non-workers in the US mean this growing group has seen particularly adverse developments in their net incomes.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Over recent decades, substantial changes in the distribution of incomes in both Great
Britain (GB) and the United States (US) have placed increased pressure on government
budgets.1 Declining employment and stagnant wages – each of which have affected both
countries, to different extents and at different times – translate into reduced tax
collections, while increased eligibility for and generosity of social insurance, means-
tested transfer payments and work-based credits result in greater expenditures. The latter
trend has been reinforced by the interplay between the labour market and the family, with
increased inequality in family earnings and in assortative mating. The aim of this paper
is to describe the relationship between inequality in labour earnings and the evolution of
family income inequality. Tony Atkinson was the world leader in driving forward the study
of economic inequality and its development over time, see Atkinson (1970, 1982, 1993,
1997, 2005). Many aspects of the work we present here take the lead from Tony's
inspirational research in this field - in particular, the role of the tax and benefit
system in mitigating earnings inequality and the interaction between the labour market and
household income inequality, for example Atkinson (1992, 2000) and Atkinson (2006).
Changes in wage inequality have been at the centre of much empirical research in labour
economics. This includes large bodies of work aiming to identify causal channels (e.g.
Bound and Johnson (1992); Katz and Murphy (1992); Card and DiNardo (2002); Bowlus and
Robin (2004); Lemieux (2006); Autor et al. (2008); Blundell et al. (2016a, 2016b)) and to
describe in some detail the key dimensions of change (e.g. Juhn et al. (1993); Katz and
Autor (1999); Gosling et al. (2000); Piketty and Saez (2003); Burkhauser et al. (2012);
Machin (2015); Guvenen et al. (2017)). However, there has been little systematic cross-
country comparative work, and much less attention to the interaction between the tax and
transfer system and family earnings in the evolution of household inequality. Family
income inequality differs from wage inequality for a number of reasons. Family labour
income depends also on hours of work and on how hours and wages covary between spouses,
meaning the interplay between the intensive margin and jointness of the labour supply
decisions, which may be heavily influenced by assortative mating in the marriage market
(Blundell et al., 2016a, 2016b). In addition, the tax and transfer system can be a very
important bridge between family labour income and living standards, through taxes, work-
contingent credits and social assistance transfers. Tax and transfer systems are typically
quite nonlinear, especially at low-incomes, and this can lead to very different inferences
about levels of household income inequality; and major reforms to these systems can and do
have large effects on the income distribution. We examine the labour market and tax and
transfer system in its relationship with household income inequality in Britain and the US
spanning the 36 years from 1979 to 2015. The approach we take is descriptive, but informed
by structural changes in potentially-selective labour force participation, hours of work,
assortative mating and income insurance provided by the tax and transfer system across the
wage distribution. We develop an approach to study how the intensive margin of labour
supply, family structure and the tax and transfer system have interacted over time to
affect the link between wages and net family incomes right across the male and female wage
distributions. To set the scene we begin by documenting and contrasting trends in male
earnings and net (after-tax and transfer) income in each country. We then systematically
trace out the path from individual labour market outcomes through to net family incomes,
unpacking the underlying components of income inequality in the following sequence:
Employment → Wages → Earnings → Family Structure → Family Market Income → Welfare → Gross
Income → Taxes and Work-Based Tax Credits → Net Income. We explicitly consider the link
between employment and wages with a median selection approach to bound wages in an effort
to address selection into, and out of, the labour force, which has likely changed very
differentially between the two countries over time (Johnson et al., 2000; Chandra, 2003;
Blundell et al., 2007). In terms of the labour market, taking a relatively long-term view
and considering trends since 1979, the basic background facts are that real wages have
grown far less in the US than in Britain – and in fact have not grown at all at the median
except for college graduates – while employment trends have looked relatively similar.
However, over the past two decades, and especially since the Great Recession, employment
has been more robust in Britain while wages have been more robust in the US. Britain has
seen a large increase in male earnings inequality, not just during the much-documented
1980s inequality boom, but also since then. The increase over the past two decades was
driven by a broadly secular decline in the hours of work of men at lower wage percentiles:
inequality in male hourly wages between the 5th and 95th percentile changed little. The
hours of work story has been the opposite among British women, among whom increases at the
bottom of the wage distribution have reduced earnings inequality. This has not been
enough, however, to stop family earnings inequality from rising. In the US, secular trends
in hours worked (among workers) have been less pronounced, albeit with considerable
cyclical variation around that, but male hourly wage inequality has increased. Meanwhile,
employment among less-skilled men in the US fell over the sample period, and since 2000
has even fallen among higher-educated, and remarkably for women of all skill levels after
a secular increase in the prior three decades. Using a bounding approach to account for
the potential effect of selective entrances and exits from the labour market, we show that
– especially since the Great Recession – wage trends among lower-educated groups may be
more similar between the two countries than the raw data focused only on workers imply.
Nevertheless, the basic qualitative comparisons between the countries prove robust to this
bounding exercise. Even though there were sharp declines in hours of work among men in
Britain, and some increase in assortative mating, the British welfare state has stabilized
the economic inequality of tax units across the most of the net income distribution over
the past two decades. For example, we show that 90/10 net income inequality fell slightly
in Britain from 1994 to 2015 even though male earnings inequality increased. In
comparison, we show that in the US 90/10 net income inequality rose sharply, suggesting
that the US tax and welfare system is less successful at counteracting changes in the
labour and marriage markets. The greater stabilization in Britain did come at a
considerable fiscal cost, in particular due to large increases in the generosity of tax
credits in the late 1990s and early 2000s which led to these credits trebling as a share
of GDP from 0.5% in 1997 to 1.5% in 2004.2 The paper proceeds as follows. Section 2 gives
a brief overview of the key policy context in both Britain and the US. Section 3 discusses
the data we use in the paper, including how we harmonize the measurement of key variables
across countries to the extent possible. Section 4 sets out the context of overall changes
in net family income inequality in both countries, and how this relates to male earnings
inequality. We then unpack the links between these. Section 5 begins with the labour
market, including how it interacts with the marriage market, while Section 6 examines the
impact of the tax and transfer system. Section 7 then brings these together by
systematically tracing the links from wages right through to net family incomes. Section 8
concludes.

<h>THE POLICY CONTEXT</h>
------------------

During the period considered in this paper there have been a number of key policy changes
in both countries that are relevant for our analysis. In Britain there were significant
cuts to income taxes during the 1980s, especially for higher earners. The top marginal
income tax rate fell from 60% to 40% in 1988, and the basic rate of income tax fell in
stages through the decade from 30% to 25%. Since 1994, which – for data reasons – we focus
on for much of the analysis, the basic rate of income tax has fallen further in a number
of incremental steps to 20%, and since 2011 the zero-rate band has been expanded rapidly.
However, fiscal drag and some discretionary policy changes have pulled many more
individuals into the higher tax bracket: the number paying the marginal rate of at least
40% has more than doubled since 1994.3 The net result is that the income tax system has
become more progressive in recent years (with the opposite having happened in the 1980s).
Since the late 1990s much of the key policy change in Britain has been on the transfer
side. The Labour governments of 1997 to 2010 presided over large increases in the
generosity of social assistance and tax credits, in large part as a means of pursuing
ambitious quantitative child poverty targets for 2010 and 2020 (Joyce and Sibieta, 2013).
The term ‘tax credits’ in Britain is in fact used to describe two very different forms of
support: a genuinely work-contingent transfer4, currently named Working Tax Credit (WTC),
and an additional means-tested element specifically for families with children (Child Tax
Credit, CTC) which is available – since 2003 – to low-income families irrespective of work
status. The out-of-work safety net was also made significantly more generous for families
with children under Labour. Since 2011, however, a broad-based set of cuts to means-tested
working-age transfers have been implemented as part of post-recession fiscal consolidation
measures. These are clearly evident in the analysis we present later up to 2015, but they
continued after that and are set to continue for several more years. Another important
policy change in Britain was the introduction of the National Minimum Wage in 1999. It was
subsequently increased in several stages, and by 2015 (the end of our period of analysis)
it covered around 4% of employees. It is, however, now being extended much further and is
set to cover around 12% of employees by 2020 (Cribb et al., 2017). Like Britain, the
economic landscape of the United States over the past several decades has been
characterized by massive changes to tax and welfare policy. The Economic Recovery Tax Act
of 1981 and the Tax Reform Act of 1986 jointly broadened the tax base and reduced the
number of federal income tax brackets from 16 to four, with the marginal tax rate on the
highest income earners dropping from 70% to 28% by 1989 (Auerbach and Slemrod, 1997;
Burman et al., 1998; Kniesner and Ziliak, 2002). The subsequent tax changes over the
ensuing two decades eventually led to a return to seven marginal tax brackets and a top
rate of 39.6% by 2009. Although the tax reforms expanded the standard deduction and
personal exemption amounts, and thereby removed several million low-income households from
the federal tax rolls, there were strong incentives for these families to file in order to
claim refundable tax credits for workers; namely, the Earned Income Tax Credit (EITC) and
the Additional Child Tax Credit (ACTC). The EITC was created in 1975 and targeted to low-
wage workers (Nichols and Rothstein, 2016). The generosity was expanded several times in
the 1980s and 1990s, and by 2014 the maximum credit was $5460 for a family with two
qualifying children and annual earnings under $17,580. Over 28 million taxpayers claimed
the credit that year at a current-year cost of over $68 billion, or 0.4% of GDP. The non-
refundable Child Tax Credit and refundable portion ACTC were established in 1997 and
(currently) provide a credit against tax liability of $1000 for each child under the age
of 17. Initially eligibility was restricted to workers with annual earnings in excess of
$10,000 in 2001 (and indexed to inflation thereafter), and most benefits went to the
middle and upper-middle class. As part of the 2009 response to the Great Recession, the
eligibility limit was lowered to $3000, thus better targeted the ACTC to part-time and
part-year low-income workers. By the 2014 tax year, expenditure on the ACTC program
exceeded $30 billion, or 0.2% of GDP. Concomitant with falling marginal income tax rates
and expanding credits were substantial expansions in the payroll tax, which is used to
finance Social Security retirement benefits, disability benefits, and Medicare health
insurance for the elderly and disabled. While the rates have not changed since 1991 (15.3%
combined employer/employee rate), the base applicable to Medicare tax (2.9 percentage
points of the 15.3) was uncapped that year, and the retirement and disability benefit base
subject to taxation was indexed to inflation and by 2014 was $117,000. Alongside the major
changes to tax legislation were wholesale changes to means-tested transfers during the
1990s. The reforms altered significantly the economic rewards to work and to participation
in transfer programs, and affected all segments of the low-income population. Some
programs retrenched, while others witnessed dramatic growth (Ziliak, 2015). The 1996
Personal Responsibility and Work Opportunity Reconciliation Act abolished the cash welfare
program Aid to Families with Dependent Children, which was an entitlement program for low-
income and low-asset (single-mother) families with children under age 18, and replaced it
with the time-limited, block-grant program Temporary Assistance to Needy Families (TANF).
TANF limited eligibility to no more than five years, and less at state discretion, and
imposed work requirements and numerous other restrictions on eligibility (Ziliak, 2016).
While this program change effectively eliminated out-of-work cash welfare in the US, since
2000 there was huge growth in food assistance spending from the Supplemental Nutrition
Assistance Program (aka food stamps), in health insurance coverage for children—first with
state-directed Medicaid expansions, then federal creation of the Supplemental Children's
Health Insurance Program, and finally the 2014 rollout of the Affordable Care Act—and
steady growth of disability benefits both related to work (Disability Insurance) and
childhood (Supplemental Security Income). Taken together, inflation-adjusted spending on
the major US social insurance and means-tested transfers grew 60% to over $2 trillion by
2010, or over 13% of GDP (Ziliak, 2015).

<h>DATA</h>
----

We begin by providing a brief overview of our data sources, followed by a detailed
description of how the various labour market and income sources were measured. We
endeavoured to the extent possible to harmonize the datasets across countries over the
past three and a half decades to provide a consistent and comprehensive portrait of the
economic circumstances of individuals and their families in Britain and the United States.

<hs>  Great Britain</hs>
  ~~~~~~~~~~~~~

For the research on Britain, we draw on two distinct sources of data: the 1979–1993 survey
years of the Family Expenditure Survey (FES), and the 1994–2015 survey years of the Family
Resources Survey (FRS).5 Both datasets are annual household surveys and are commonly
combined in this manner, including in the calculation of official statistics on poverty
and inequality. The FES and FRS collect data on various sources of income received and
taxes paid close to the time of interview, and all income and tax amounts are based on the
self-reported values. A very small fraction of income components (typically less than 1%)
suffer from non-response and any missing values are imputed. However, as neither survey
identifies the observations and income components that have undergone imputation, we are
unable restrict our sample to those without any imputed information. We restrict our
sample to men and women aged 25–55 to focus on the prime working-age population, and
thereby abstract from the part of the lifecycle where most human capital investments occur
and that part associated with retirement.

<hs>  United States</hs>
  ~~~~~~~~~~~~~

For the US analysis, we use the Current Population Survey Annual Social and Economic
Supplement (ASEC) for the 1980–2016 survey years. The ASEC is a stratified random sample
of 60,000–90,000 household addresses from the noninstitutionalized population in the US.
It serves as the official source of income and poverty statistics and has been the
workhorse dataset for research on wage and income inequality. As with the British data, we
restrict our focus on men and women aged 25–55. However, there are some important
distinctions in the ASEC. First, all information refers to prior calendar year rather than
the time immediately prior to the interview, as in the British data. Second, taxes and tax
credits are self-reported in the British data, whereas the ASEC does not collect tax
information. Instead we run the ASEC data through NBER's TAXSIM simulation program, which
assumes 100% take-up among those eligible for tax credits. Third, nonresponse to earnings
questions, and to the entire ASEC altogether, has been on the rise (Bollinger and Hirsch,
2006; Bollinger et al., 2017), and the US Census Bureau imputes values to nonrespondents.
We drop those with imputed earnings and hours and reweight the ASEC data as described
below.

<hs>  Measuring labour-market outcomes and incomes</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The primary economic outcomes in our analysis are employment, hours, real earnings and
wages, and real before-tax gross income, and real after-tax and transfer (net) income.

     <hss>Employment rate</hss>

        In the British data, we measure the employment rate as the fraction of the
        population aged 25–55 employed during the survey week (sometimes referred as
        employment per capita). The measure is the same in the US, except employment is
        for any time in the prior year.

     <hss>Hours of work</hss>

        In both countries, hours of work refers to usual hours worked per week, where the
        reference period in Britain is “typical” hours in the current financial year,
        while in the US it is typical hours in the prior year. The data from Britain
        distinguishes between paid ‘basic’ and both paid and unpaid overtime hours. The
        hours measure we use is defined using paid basic and paid overtime hours only in
        order to more accurately reflect trends in formal labour market arrangements. No
        such distinction is made in the US. Overtime hours in the US primarily only apply
        to workers paid by the hour, and those workers are eligible to be paid 1.5 times
        the normal hourly wage.

     <hss>Real earnings and wages</hss>

        In the British data, information on earnings is obtained by asking respondents the
        amount they were paid on the pay date closest to interview. Raw responses are
        converted into nominal weekly amounts and we additionally convert these nominal
        values to real terms using a modified Consumer Price Index that includes an
        adjustment for mortgage interest. In the US, earnings are measured for the past
        year, and deflated by the Personal Consumption Expenditure Deflator. In both cases
        we use a 2010 base year. Real hourly wages are constructed as the ratio of weekly
        real earnings and usual hours per week in Britain, and the ratio of real annual
        earnings to annual hours of work (hours per week times number of weeks worked). We
        leave each country's earnings and wages in their respective currencies. For the
        analysis that relies on wage information, we exclude those with extreme gender-
        specific real average hourly wages (below 1st percentile; above 99.9th percentile)
        and adjust the survey weights using inverse probability weighting. Specifically,
        for each gender and year, we estimate a saturated probit model of the probability
        of not having an extreme wage using levels and interactions of age, race,
        education, marital status, and other demographics. We then divide the survey
        weight by the fitted probability of not having an extreme wage. For the US, we
        modify the procedure to also account for non-imputed employment and earnings. The
        reweighting approach results in consistent estimates under the assumption that the
        excluded observations are missing mean conditional at random. As we describe in
        the results section, this assumption is relaxed when we bound the wage series with
        worst-case bounds to account for possible nonrandom selection into employment.

     <hss>Gross and net income</hss>

        As we are ultimately interested in changes in family-level outcomes, in addition
        to individual-level employment and earnings we also construct gross and net income
        at the tax unit level. Tax units in the Britain are defined as an adult, their
        partner (married or unmarried), and any dependent children in their care. In the
        US data they are inferred from household relationship pointers and ages of
        occupants, where unlike Britain, cohabiting partners in the US do not file
        jointly.6 Our measure of gross income includes the earnings of the primary and
        secondary earner (if present), transfer income and nontransfer nonlabour income
        such as rent, interest, and dividend income. In the British data, transfers
        include all cash transfers and work-based tax credits, including the Child and
        Working Tax Credits, Child Benefit, Housing Benefit, Income Support and
        unemployment and disability benefits. For the US data, transfers include Social
        Security, Disability Insurance, Unemployment Insurance, Workers Compensation,
        Supplement Security Income, Temporary Assistance for Needy Families (cash only),
        Supplemental Nutrition Assistance Program (food stamps), Earned Income Tax Credit,
        and the Additional Child Tax Credit. Some of the benefits are recorded in the
        surveys at the individual level, and others at the family level. For the former we
        sum them up across all individuals in the tax unit. For both countries we rely on
        self-reported information when calculating transfer income (in the US, the EITC
        and ACTC are simulated with TAXSIM). In both the FES/FRS and the ASEC this
        approach is known to lead to systematically lower spending estimates than those
        observed in administrative data (Meyer et al., 2015; Brewer et al., 2017). While
        our main analysis does not account for such under-reporting, we provide additional
        results that adjust the self-reported benefit income amounts to match totals taken
        from administrative data and show headline trends are robust to this. Net income
        is constructed as gross income less tax payments, which in the British data
        includes income tax, employee National Insurance Contributions, and Council Tax.7
        As noted previously, tax payments and credits are not reported in the US data and
        must be simulated. The NBER TAXSIM program receives as inputs the tax unit marital
        status, ages of members, number of (child) dependents for (refundable) tax
        credits, earnings, taxable and nontaxable transfers, and other items. It then
        returns a simulated estimate of federal, state, and payroll tax liability,
        inclusive of tax credits. For the payroll tax, we just assign the employee share.
        Finally, because household size and composition has changed substantially in both
        countries in recent decades, we equivalise gross and net income using a modified
        OECD scale.8

     <hss>Education</hss>

        For many of our outcomes we split the sample into education groups, which is a
        standard proxy for skill and/or permanent income. Variables related to educational
        attainment in the British surveys have changed over time. In order to create a
        continuous time series we therefore focus on school-leaving age, which is
        consistently recorded over the entire 1979–2015 period, and use this indicator of
        education to define four groups: left education aged 16 years or younger; left
        aged 17 or 18; left aged 19 or 20; and left aged 21 or older. These age categories
        roughly approximate the four US education groups of less than high school, high
        school graduate (or General Equivalency Degree), some college (includes community
        college and associates degrees), and four-year college or more. Importantly,
        however, those leaving school at age 16 in Britain receive credentials, whereas
        they do not in the US, and thus the low-educated group in Britain likely has more
        qualifications than the typical US “dropout”. Appendix Fig. 1 demonstrates that
        there has been substantial education upgrading in both countries since 1979, with
        a reduction in half of the lowest education group. In Britain, 80% of men and
        women left school by age 16, and this plummeted to 40% by 2015. The comparable
        percentages in the US were roughly 20 and 10%, respectively. Notably, the most
        marked growth in both countries is the highest education level, especially among
        women when 35 (40)% of British (US) 25–55 year olds attained the equivalent of
        college or more in 2015, double the rate in 1979.

     <hss>Marital status</hss>

        The remaining key demographic outcome that factors prominently in our analysis is
        marital status. In the British data, couples who are married cannot be
        distinguished from those who are cohabiting, while in the US data cohabiting
        couples are treated as unrelated individuals and marriage only refers to those
        couples in a legally recognized union.9 Appendix Fig. 2 presents trends in the
        fraction of men and women married (or cohabiting in Britain) by the four education
        groups. The substantial retreat from marriage is most evident among the least
        skilled, especially men in the US. In 1979, the fraction of married US men with
        high school or less was just under 80%, and greater than the fraction married
        among those with a college degree. By 2015, the fraction of high school graduates
        or dropouts who were married was nearly 20 percentage points lower than that of
        college educated men. Similar patterns hold among US women, and both British men
        and women, though they are much more attenuated in Britain.10

<h>HOUSEHOLD INCOME INEQUALITY</h>
---------------------------

Net income among ‘working age families’ in Britain (denoted as G.B. in all figures) and
the US is presented in Fig. 1. It shows strong growth from 1979 to 2015 in household
income across the distribution in Britain, and for the top half of the distribution in the
US, though relatively flat net incomes in the bottom half, except for the brief window in
the late 1990s. The experience in the two countries during the Great Recession, however,
was markedly different. Real net incomes fell sharply in Britain, especially in the upper
percentiles, while they continued to keep pace with inflation in the US. Although the top
of the income distribution has grown considerably since the mid-1990s in both countries,
Fig. 2 shows that the 90/10 ratio of net income inequality has been stable in Britain over
this period, while increasing steadily in the US since 2000 (largely due to a rise in the
90/50 not shown in the figure). The British experience of stable 90/10 net income
inequality stands in stark contrast to the sharp rise in male (individual) earnings
inequality. This suggests the insurance against relatively weak earnings growth provided
by family structure and the tax and benefit system may differ substantively from the US
where earnings inequality has increased alongside net income inequality. Fig. 2 also
highlights that male earnings inequality is much more volatile in the US than in Britain,
which as will be seen below, reflects much greater cyclical sensitivity in hours of work,
especially among low-income workers. To verify the trends in net income growth and in net
income inequality documented here are robust to potential under-reporting of transfer
income, Appendix Figs. 3 and 4 repeat the analysis shown in Figs. 1 and 2 using a measure
of net income that rescales transfer income to match transfer spending totals taken from
administrative data.11 Appendix Fig. 3 shows this adjustment leads to slightly stronger
net income growth at the bottom of the distribution in both countries. Appendix Fig. 4
shows 90/10 net income inequality in both countries is slightly lower when one accounts
for under-reporting of transfer income, although trends in inequality are broadly similar
to those shown in Fig. 2, particularly since 1994 which is the period we focus on in later
analysis.12

<h>THE CHANGING LABOUR MARKET AND THE CHANGING WAGE DISTRIBUTION</h>
-------------------------------------------------------------

The dramatic differences in Britain and the US in terms of overall after-tax and transfer
income inequality, in contradistinction to the rising male earnings inequality in both
countries, forms the basis for the ensuing analysis, where we first examine differences in
employment and wages in each country.

<hs>  Employment, hours and wage inequality by gender, education and race</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Fig. 3 sets out employment rates over time in both countries, by gender and education
level. Comparing levels of employment, perhaps the most striking difference is how much
larger the gap between the highest- and lowest- educated is in the US than in Britain –
especially for women. Part of this difference is explained by the fact discussed in
Section 3.3 that the lowest education group in the US are less likely to have obtained
formal educational qualifications than the equivalent group in Britain. Looking at trends
over time, male employment rates in both countries are lower than they were in 1979,
especially for the lowest educated. However, in the US this is driven by a broadly secular
decline since around 1990. In Britain, by contrast, male employment has been on an upward
trend since the early 1990s (punctuated temporarily by the Great Recession), after falling
sharply through much of the 1980s and during the early 1990s recession. The result has
been a marked convergence of male employment rates in the two countries over the past 25
years, from a starting point at which male employment in the US had been considerably
higher for all but the lowest educated. Among women, employment was stable or gently
rising in both countries during the 1980s, but again it has since been in secular decline
in the US – especially for the lowest-educated – while remaining stable or increasing
slightly in Britain. Over approximately the past 25 years, trends in employment have been
much more robust in Britain than in the US and this has been especially evident since the
Great Recession. Appendix Fig. 5 documents further heterogeneity in employment trends by
disaggregating by race and education groups.13 This shows the employment rate of less-
skilled non-white men in both countries is substantially lower than the rates observed
among other groups of men, especially in US. Higher-educated black men have employment
rates comparable to high school dropout white men in the US, and the gap between both of
those groups and higher-educated white men has expanded in the last decade. Remarkably,
there is no race gap in employment for US women, only a gap based on education attainment.
It is not just the extensive margin of employment that has been important in driving
changes in incomes and inequality. Fig. 4 documents mean hours of work among workers in
the two countries over time, split by gender and education. The figure shows a large
difference between the US and Britain in the patterns of male employment at the intensive
margin across skill groups with higher-educated men working far more hours than the low-
educated in the US and vice versa in Britain. However, this contrast is in part due to
differences in the treatment of unpaid overtime in the hours measure used in each country,
as discussed in Section 3.3. Specifically, accounting for unpaid hours worked in Britain
leads to the same ranking of education groups observed in the US, as unpaid work increases
the average hours worked by the highest education group while leaving average hours of
lower-educated workers largely unchanged. For women the relativities across skill groups
are the same in both countries, with higher educated women working more hours; but US
women work considerably more hours than their British counterparts, on average. Among
women, average hours of work have been quite stable in both countries in recent decades,
after rising during the 1980s. The one exception is the lowest-educated women in the US,
whose hours of work have fallen since the mid 2000s. For men the key pattern has been a
large convergence in hours of work across education groups in Britain. This has been
driven by particularly large falls in hours among the lower-educated. Appendix Fig. 6
provides some detail behind this, showing percentage point changes in rates of “mini-jobs”
(less than 16 h per week), part-time work (less than or equal to 30 h per week) and
especially long hours of work (greater than 45 per week) between 1994 and 2015 across the
hourly wage distribution. This highlights that reductions in hours of work among British
men are in fact particularly concentrated in the bottom quintile of the hourly wage
distribution and have been driven by both a reduction in the prevalence of long hours and
an increase in the prevalence of part-time work. There has also been a sharp fall in the
prevalence of “mini-jobs” among women in the bottom quintile of the wage distribution in
Britain.14 By contrast, the hours changes among men and women in the US have been far more
uniform across the wage distribution. Following from these changes in employment, Fig. 5
shows how median real hourly wages among those in paid work have developed for the
different education groups. The significant contrasts in employment trends between the two
countries suggest the observed wage trends may be in part driven by trends in the
selectivity of the workforce. To account for this, we implement a modified version of the
median selection model (see, e.g. Johnson et al., 2000; Chandra, 2003; Blundell et al.,
2007) which bounds wage trends by assuming that all changes in employment rates are the
result of entrances and exits at the bottom of the within-group wage distribution.15 The
bounded series are indicated by dashed lines. The US has seen a remarkably long period of
real wage stagnation, stretching back over most of the period since 1979, with the only
clear exception being a short period during the boom of the late 1990s. In fact, for men
it is only college graduates among whom median real wages are currently any higher than in
1979. The bounded series confirm that accounting for trends in selectivity would only make
this conclusion stronger, due to large employment declines among lower-educated men over
this period. In Britain, wage growth was considerably more robust until the early 2000s.
The more recent comparison is different. Since the mid 2000s, and especially the Great
Recession, Britain has seen marked declines in median hourly wages across most groups (but
less so among the lowest educated). These wage trends tend to be worse than seen among
similar groups in the US over the same period. It does, however, turn out to be quite
important to assess employment and wage trends, and the link between them via selection,
in a coherent framework. The potential for wage trends among less educated US men to have
been flattened by selection (due to falling employment) in recent years is significant,
and the bounded series show falls in wages more in line with their British counterparts.16
Nevertheless, overall Figs. 3–5 show a stark difference in the nature of the impact of the
Great Recession on the US and British labour markets. Employment has proven more robust in
Britain, on both the extensive and intensive margin, particularly through the pace with
which employment rates recovered after the initial shock. By contrast much more of the
adjustment in Britain has come through lower real wages, especially for the high educated.
These developments resulted in the post-recession decline in top net incomes in Britain as
shown in Fig. 1, while they reinforced pre-existing trends towards higher inequality in
the US. In combination, these trends in wages and hours of work have led to increased male
and reduced female earnings inequality in both countries. This is depicted in Fig. 6,
which highlights just how influential intensive margin trends have been in Britain as the
growth in male (female) earnings is far greater towards the top (bottom) of the
distribution than growth in wages. In the US, however, the close alignment between growth
in wages and earnings across the distribution suggests that changes in earnings inequality
are primarily due to changes in wage inequality, rather than trends in employment on the
intensive margin.17 To assess the relative importance of wage and hours trends more
formally, we decompose the change in the log of individual weekly earnings into components
that are attributed to changes in the variance of log hours and log wages and the
covariance between log hours and log wages.18 Table 1 reports the results of this
decomposition separately for men and women in each country over three periods: 1994–2015,
1994–2007 and 2007–2015. The first two panels of Table 1 confirm that male earnings
inequality has risen in both Britain and the US over the 1994–2015 period, with the rise
in Britain almost three times as large as that in the US (an increase of 0.103 compared to
0.035). One reason for this difference is that earnings inequality among British males
rose consistently over the entire period, whereas in the US it was largely unchanged
between 1994 and 2007 before increasing during the period after the financial crisis. This
reflects Fig. 2, which showed a secular increase in the British male earnings 90/10 ratio
compared to a far more cyclical trend in the US 90/10. The right-most three columns of the
table show that increases in the variance of wages and the covariance between hours and
wages are both important drivers of the rise in male earnings inequality in Britain,
accounting respectively for 49.7% and 44.7% of the overall increase in the variance of
earnings. Although the covariance between hours and wages has had a substantial impact on
US male earnings inequality, the variance of wages is more important and accounts for over
two-thirds of the increase in the variance of earnings over the 1994–2015 period.19 In
contrast to the rise in male earnings inequality, the third and fourth panels of Table 1
show falls in female earnings inequality across countries. The magnitude of the change is
again greater in Britain than the US (a reduction of 0.105 compared to 0.02), and is
primarily due to reductions in inequality that occurred in the pre-recession 1994–2007
period. In both countries, these reductions have been driven by falls in the variance of
weekly hours. In Britain this has been reinforced by a reduction in the covariance between
hours and wages, whereas in the US hours and wages among women have become more positively
correlated. In summary, something has happened in Britain in recent decades which goes
against the conventional wisdom that male employment at the intensive margin is relatively
fixed. The breakdown of this rule has had first order effects on earnings inequality in
Britain. In a comparative context it tempers the conclusion that one would reach when
focusing on the extensive margin alone, which is that male employment has been on a worse
trajectory in the US with a particular problem among the lowest skilled. The British story
becomes more reminiscent of the US story once the intensive margin is incorporated.
Belfield et al. (2017) have shown that the increase in part-time work among low-wage
British men has occurred among single men and those in couples, and those with and without
children. Explaining the origins of this change, and in particular whether it represents a
demand-side or supply-side shift, is a key challenge for future research given its
implications for welfare and potential possible policy responses. A satisfying explanation
would need to account for why Britain has not seen similar concurrent changes at the
extensive margin, and why the adjustments in this respect have been the opposite of those
in the US.

<hs>  Marriage and assortative mating</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We now make the important move from individual labour market outcomes to family-level
outcomes. A key part of this link is the pattern of assortative mating, which is examined
in Figs. 7 and 8. For each country and gender we rank by percentile of individual hourly
wages and plot changes in spousal characteristics within each percentile group, comparing
1994 with 2015. In Britain, but not the US, we are able to observe non-married cohabiting
partners – though for parsimony we use the term “spouse” to cover any cohabitation between
partners. Although this introduces an inconsistency in measurement between countries,
long-term non-marital cohabitation is comparatively less common in the US. Appendix Fig. 2
showed that living as part of a couple has generally become less common across education
groups in both countries, while Fig. 7 shows that these changes are pervasive across the
majority of the wage distribution. It also shows that this change has tended to be more
pronounced for people in the bottom half of the gender-specific hourly wage distribution,
and even more pronounced among non-working men (as indicated by the dots on the left-hand
side of each panel). Changes in the probability of having a working spouse exhibit a
similar gradient across the wage distribution. The gradient here is especially strong for
women. In Britain the probability of having a working spouse has tended to decline in the
bottom half of the female wage distribution and to increase in the top half. In the US, it
has declined throughout essentially the entire distribution, but by more towards the
bottom. Fig. 8 examines how the within-family correlation between wages has changed since
1994, plotting the average wage percentile rank of spouses by own-wage percentile (for
those in each percentile group who have a working spouse). For both countries and genders,
there is a clear positive correlation: people further up the individual wage distribution
tend to have spouses who, if in work, are also further up the wage distribution. In the
US, but not Britain, there is also clear evidence of an increase in this form of
assortativeness as the gradient has become steeper over the past two decades.20 Table 2
shows inequality in total earnings among dual-earner couples has increased in both Britain
and the US. In the British case, the increase is predominantly due to an increase in
earnings inequality among the higher-paid member of the couple. Since main earners are
overwhelmingly male, this result mirrors the rise in male earnings inequality documented
above. Increases in the covariance between main and secondary earner pay have also acted
to push up tax unit earnings inequality, particularly in the non-extreme section of the
distribution, which indicates that two-earner couples in Britain have become increasingly
assortative over the last two decades. The US results show tax unit earnings are more
unequal than in Britain. Comparing the trimmed and untrimmed samples in the US reveals
that increases in inequality among main earners has been entirely driven by the tails of
the distribution: trends in main-earner inequality have actually acted to reduce tax unit
earnings inequality among the middle 90%.22 Trends among secondary earners have acted to
increase total earnings inequality in the US – due to both an increase in I2 inequality in
their earnings and an increase in their share of total tax unit earnings – whereas they
have slightly reduced inequality in Britain. Finally, Table 2 shows that increases in
assortativeness have made a greater contribution to rising inequality in the US than in
Britain, which mirrors the pattern shown in Fig. 8.

<h>THE TAX AND WELFARE SYSTEM</h>
--------------------------

Another key bridge between individual labour market outcomes and family incomes is the
government transfer and tax credit system. It makes sense to analyse this when moving to
the family level: eligibility for such transfers is typically assessed at that level and
so, at least where resources are pooled within families, transfer program participation
measured at the individual level is not as meaningful. Fig. 9 documents trends in the
generosity of the transfer systems of both countries by plotting the average share of
family gross income that comes from the transfers and in-work tax credits by gender and
education. The figure makes evident the greater generosity of the British welfare system
across the education distribution in comparison to the US system, at least until most
recently, with transfers and in-work tax credits accounting for a higher share of gross
income among men and women of all education levels in Britain. This is in spite of the
fact that, as discussed above, the lowest education group in the US is likely to be far
less skilled than the lowest education group in Britain. The figure also shows the average
generosity of the welfare system has tended to increase over the past 20 years in both
countries, particularly among the lower educated in the US.23 The impact of the Great
Recession on transfer income is also clearly shown. The increases in average welfare
receipts in Britain that occurred in the years immediately following the financial crises
have since been offset owing to the post-recession fiscal consolidation, which began in
2011 and included cuts to many transfer programs. The dramatic increase in average
transfer generosity in the US emerged in response to the Great Recession – increasing
average payments by 50% among the least skilled, but also more than doubling among those
with some college – and unlike Britain, have remained elevated through the six years
following the official end of the recession.

<h>FROM WAGES TO HOUSEHOLD INCOME INEQUALITY</h>
-----------------------------------------

Bringing together the individual labour market outcomes, assortative mating and trends in
welfare income, and adding in taxation, we can then trace the links from individual wages
right through to net family incomes. To illuminate this, in Fig. 10 we rank people
according to their position in the gender-specific hourly wage distribution and, keeping
that ranking fixed, examine changes in different measures of income over the 1994–2015
period. The figure also shows growth in the different measures of income for non-workers
which, as documented above, now account for a greater share of the working-age US
population than in 1994. We start with family labour income, cumulatively add in work-
based credits and then all other transfers (to make “gross income”), before subtracting
direct taxes (to make “net income”). Family incomes are equivalised throughout this
exercise in order to account for changes in family size and structure. The broad pattern
in family labour incomes is one of increased inequality between higher- and lower-wage
individuals, with the exception of the bottom male wage quintile in the US. These patterns
are in line with the trends already documented in male earnings inequality (male earnings
remain the dominant source of family labour income, on average) and the supporting role
played by increases in assortative mating. However, important differences emerge between
Britain and the US when looking beyond labour income. Transfers and taxes have had
significant effects on trends in inequality between high- and low-wage people in Britain,
but virtually no discernible impacts on those trends in the US. Work-contingent transfers
actually have little to do with this, as they remain only a relatively small part of the
overall transfer system in Britain (even for people in work). But increases in the
generosity of the transfer system more generally, most importantly through CTC (most of
which goes to families in work), have pushed the rate of growth in family gross income at
the lower end of the wage distribution above the rate of growth in labour income alone.
Direct tax cuts have had a further, similar impact towards the bottom, as the zero-rate
income tax band has been increased sharply since 2010. Another striking point of contrast
between Britain and the US is the experience of non-workers (represented by the dots on
the left side of each panel). In Britain their net family incomes have grown robustly over
the past 20 years, and more quickly than for the majority of the wage distribution.
Unsurprisingly this is again due to increases in the generosity of the transfer system,
particularly for families with children, both through CTC and through increases in the
rates of out-of-work transfers. In the US, by contrast, non-workers have fallen further
behind those in work over the past 20 years and in fact have seen barely any income growth
at all, although the figure does suggest that growth in welfare income has mitigated to
some extent the reductions in labour income among non-working US women. Appendix Figs. 9
and 10 repeat the analysis of Fig. 10 separately for singles and couples and those with
and without children. These additional figures reveal that growth in total labour income
has been more unevenly spread across the wage distribution among couples, re-emphasising
that changes in the assortativeness of marriage have been an important driver of income
inequality over the last two decades. The equalizing effect of changes in transfer income
is most pronounced among those with dependent children, which is to be expected as the
major welfare policy reforms in both countries have explicitly targeted this group.
Overall, Table 3 shows the gap between net income inequality in Britain and the US has
widened over the last two decades. The squared coefficient of variation in net income was
around 23% higher in the US than in Britain in 1994, whereas in 2015 it was almost 40%
higher. The most recent comparison shows that inequality in labour income is higher in the
US and is offset to a far lesser extent by transfer and credit income.

<h>CONCLUSIONS</h>
-----------

Both Britain and the US have witnessed secular increases in 90/10 male earnings inequality
over the last three decades. Up until the 1990s this was accompanied by similar increases
in 90/10 inequality in net household incomes in both countries but since then trends have
diverged with inequality in net family income declining in Britain while continuing to
rise in the US. This paper has sought to shed light on the reasons for this divergence,
taking inspiration from Tony Atkinson's extensive work on inequality, which emphasized the
importance of accounting for the interplay between inequality in the labour market, the
tax and benefit system and household income inequality. Since 1979, there have been
sizeable changes in male and female employment in both countries. These employment changes
have primarily occurred on the extensive margin in the US, with employment declining
across gender and education groups from around 1990. In Britain, by contrast, the biggest
changes have occurred on the intensive margin, with male workers experiencing declines in
average hours of work that have been steepest for the lower-educated and most pronounced
in the bottom quintile of the wage distribution. The impact of these trends in employment
and hours on family-level income inequality has been mediated through several channels.
First, changes in individual-level earnings inequality will also be influenced by changes
in wage inequality. We find that wage growth has been relatively equal across the main
part of the gender-specific wage distributions of both countries, although a novel worst-
case bounding approach suggests that reductions in employment in the US may have
attenuated growth at lower percentiles of the US wage distribution. As a result, the
intensive margin changes observed in Britain led to a sharp reduction in female earnings
inequality but a sharp increase in male earnings inequality. Second, the link between
individual-level earnings and family-level labour income depend on changes in family
composition and marital sorting. Focussing on the period since 1994, we find that both in
Britain and the US, reductions in marriage have been greatest among low-wage workers and
non-workers. In addition, the US has experienced an increase in assortative mating in
terms of the correlation between wage percentiles of both members of a couple. The result
of these trends has been an increase in inequality in family labour income among men and
women in both countries. The most important final link from family labour income and net
income is the tax and benefit system. Indeed, we find that the divergent trends in net
income inequality in Britain and the US are largely due to the different policy regimes.
Specifically, increases in the generosity of transfer payments in Britain under successive
Labour governments between 1997 and 2010 boosted net income growth among low-wage workers
and non-workers thereby equalizing growth rates in net income across the main part of the
wage distribution. Policy changes on this scale have not occurred in the US with the
result that the pattern of net income growth of US workers overall largely matches the
pattern of family labour income growth. Differences in welfare policy are also key to
understanding the differential fortunes of non-workers between countries. In Britain, many
transfer payments are not contingent on work and therefore non-workers have witnessed
relatively strong net income growth in comparison to workers. In the US, by contrast, a
major part of the country's ‘safety net’ is the EITC and welfare that is targeted at non-
working families has undergone successive reductions in generosity. As a result, non-
workers in the US have seen the largest average falls in their net income, which is
particularly worrying given this group now accounts for a greater share of the working-age
population than in previous decades. In summary, changes in labour market outcomes in
Britain and the US have undoubtedly influenced changes in net income inequality in both
countries over recent decades. However, the impact of labour market trends has differed
between countries both owing to differences in the nature of the trends themselves and the
way they have been mediated by the tax and benefit systems of each country. A key
difference between Britain and the US we have highlighted is the margin of employment that
has been the source of greatest adjustment. In particular, the intensive margin of British
male labour supply has become increasingly flexible over the past 20 years with low-wage
male workers in particular experiencing large reductions in hours of work. This is in
contrast to the US where the greatest change has been the reductions in extensive margin
employment, which is somewhat puzzling given the very low level of transfer income
available to non-workers in the US. Explaining the reasons for this difference is a key
challenge for future research given its implications for welfare and potential possible
policy responses.


<h>REFERENCES</h>
----------

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<ART>Inheritance and wealth inequality: Evidence from population registers
=====================================================================

Authors: Mikael Elinder, Oscar Erixson, Daniel Waldenström
DOI: 10.1016/j.jpubeco.2018.06.012
Year: 2018  |  Pages: 17-30
ASJC codes: 2002, 2003
Keywords: Bequests, Estates, Inheritance taxation, Net worth, Wealth distribution

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper uses population register data on inheritances and wealth in Sweden to estimate the causal impact of inheritances on wealth inequality. We find that inheritances reduce wealth inequality, as measured by the Gini coefficient or top wealth shares, but that they increase absolute dispersion. This duality in effects stems from the fact that even though richer heirs inherit larger amounts, the relative importance of the inheritance is larger for less wealthy heirs, who inherit more relative to their pre-inheritance wealth. This is in part driven by the fact that heirs do not inherit debts, which makes the distribution of inheritances more equal than the distribution of wealth among the heirs. Behavioral adjustments seem to mitigate the equalizing effect of inheritances, possibly through higher consumption among the poorer heirs. Inheritance taxation counteracts the equalizing inheritance effect, but redistribution of inheritance tax revenues can reverse this result and make the inheritance tax equalizing. Finally, we also find that inheritances increase intragenerational wealth mobility, but the effect is short-lived.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The evolution of wealth inequality and its determinants have received tremendous attention
in recent years. After decades of decreasing or relatively low levels of wealth inequality
throughout the Western world, wealth inequality may now be on the rise.1 A small but
growing body of research has also shown that the importance of inherited wealth has
increased recently (Piketty, 2011; Ohlsson et al., 2014). If wealthy children inherit from
wealthy parents and inheritances therefore primarily benefit a small elite, there may be a
link between increased inheritance flows and increased inequality in the wealth
distribution. In this paper, we investigate the impact of inheritances on the distribution
of wealth. Although we are not the first to address this issue, it is fair to say that a
consensus has not been reached in the literature about whether inheritances increase or
decrease wealth inequality. To the best of our knowledge, we are, however, the first to
use population-wide individual-level data on both inheritances and wealth to estimate the
causal effects of inheritances and characterize the underlying mechanisms. We also
contribute by studying the impact of inheritances on wealth mobility and the ways in which
inheritance taxation influences wealth inequality. At our disposal is a new population-
wide database that contains detailed individual-level information about the estates and
bequests of all Swedes who passed away during the 2002–2004 period. Our analysis is based
on 168,000 decedents, and of all their family and non-family heirs, comprising 475,000
individuals. The panel dimension of the data allows us to follow heirs and their
marketable net worth (which we will hereafter refer to as wealth) for several years—both
before and after they inherit. Our identification strategy relies on observing
inheritances and wealth distributions for yearly cohorts of heirs. Two different causal
effects are identified. First, we estimate a direct mechanical effect (DME), which
captures the immediate impact of inheritances, and occurs before any behavioral responses
(i.e., before heirs can consume the inheritance). Although we ideally want to evaluate
this effect by comparing inequalities just before and just after heirs receive their
inheritances, we come close to identifying this effect by comparing wealth inequality at
the end of the year preceding the inheritance year, with a measure of post-inheritance
wealth inequality, obtained by adding the value of the inheritance to each heir's wealth
in the year preceding the inheritance year. The second effect, denoted the behavior-
adjusted effect (BAE), shows that heirs may change their behaviors in response to their
inheritances, e.g., by consuming or investing part of their inheritances or by working
less. We identify this effect by using a difference-in-differences estimator, which
compares pre-inheritance inequality with post-inheritance inequality across the three
sequentially inheriting cohorts. Heirs who inherit one or two years later serve as the
control group for those who inherit in a given year. Note that our focus on heirs only is
not very restrictive because everyone will inherit at some point (although a zero amount
in some cases).2 This estimation strategy effectively removes biases stemming from
macroeconomic events that might influence wealth inequality from one year to the next, as
well as biases stemming from the aging of heirs. As pre-inheritance inequality trends are
almost perfectly parallel across inheritance cohorts, we are confident in making a causal
interpretation of the estimated effects. Our main finding is that inheritances reduce
relative wealth inequality. The direct mechanical effect works to reduce the Gini
coefficient by approximately 7%. As a point of reference, this decline is about as large
as the equalization following the dotcom crash in 2000, when the stock prices of internet
companies, presumably owned by the rich, plummeted. Examining different parts of the
wealth distribution, we find that the top decile's wealth share decreases substantially,
whereas the wealth share of the bottom half increases from a negative to a positive share.
While inheritances reduce relative inequality, we find that they increase the absolute
dispersion of wealth. This discrepancy between relative and absolute inheritance effects
exists because, while wealthier heirs inherit larger amounts, less wealthy heirs receive
much larger inheritances relative to their pre-inheritance wealth. Behavioral adjustments
appear to dilute the equalizing impact of inheritances. The behavior-adjusted effects are
generally smaller than the direct mechanical effects; for example, the Gini coefficient
falls by 4% rather than 7%. This equality-diluting effect is consistent with previous
research showing that less wealthy heirs spend a larger share of their inherited wealth
than wealthier heirs (Druedahl and Martinello, 2017). We are also able to present the
first register-based empirical estimates of how inheritance taxation affects wealth
inequality, exploiting information about actual individual tax payments.3 The results
indicate that the inheritance tax increases wealth inequality, reflecting that less
wealthy heirs pay more in taxes relative to their wealth than wealthier heirs do. Still,
wealthier heirs pay higher inheritance taxes, but their tax payments are almost always
negligible relative to their wealth. However, we show that the redistribution of
inheritance tax revenues can reverse this result and make the inheritance tax equalizing.
Moreover, we estimate the effect of inheritances on wealth mobility. The welfare
interpretation of our inequality results may partly depend on whether heirs switch places
in the wealth distribution or retain their ranks after they inherit. We find that,
overall, mobility rises substantially, with increased mobility across all parts of the
wealth distribution. A series of sensitivity checks suggest that our main findings are
robust across several dimensions. First, they do not change when the observed wealth
levels are adjusted for potential measurement errors in our wealth and inheritance data.
Second, they do not seem to be driven by unobserved inter vivos gifts from wealthy
decedents; if anything, adding estimated gifts strengthens the equalizing impact of
inheritances. Third, only analyzing inheritances from parents to their children (and
neglecting one-third of heirs with more distant family or non-family ties) has a
negligible impact on our conclusions. Fourth, we study the importance of young heirs (40
and younger), who could be driving the results because they tend to have relatively little
wealth and thus should be affected relatively more by inheriting. While inheritance
effects are indeed substantially larger in this younger group, inheritance effects are
also important among older heirs. Finally, we exploit parent-child correlations in wealth
accumulation and sudden deaths to examine whether heirs adjust their saving behaviors in
response to expectations about future inheritances. If such responses were quantitatively
important, we would miss a relevant aspect of how inheritances influence the wealth
distribution. However, we find no indications of their importance or influence in the
data. Our study contributes to the previous empirical literature on the distributional
consequences of inherited wealth.4 One group of studies uses simulation methods to model
people's savings and giving behavior to calibrate synthetic wealth and inheritance
distributions. A sweeping generalization is that these studies tend to find that
inheritances constitute a major source of wealth inequality.5 Another group uses
individual-level data on people's self-reported wealth and their receipt of gifts and
inheritances. The seminal contributions of Wolff (2002, 2003, 2015) and Wolff and
Gittleman (2014) use data from the Survey of Consumer Finances to estimate how gifts and
inheritances influence the distribution of wealth in the United States. A consistent
finding in these studies is that the rich inherit more than the less affluent, but that
the rich inherit less relative to their existing wealth, causing inheritances to have an
equalizing effect on the distribution of wealth. Similar equalizing effects of
inheritances are found in survey data from the United Kingdom (Karagiannaki, 2015;
Crawford and Hood, 2016), Japan (Horioka, 2009), Sweden (Klevmarken, 2004) and eight EU
countries (Bönke et al., 2017). In a study closely related to ours, Boserup et al. (2016)
examine Danish individual-level tax register data on wealth to estimate the effect of
inheritances on wealth inequality. The identification of the effect is based on following
the wealth of children (45 to 50 years old) before and after the demise of their parents
and then comparing this evolution to the wealth of similarly aged children whose parents
did not pass away during the study period. The main findings are similar to ours, that is,
inheritances cause an increase in the absolute dispersion of wealth and a decrease in the
relative wealth inequality. They find larger equalizing effects than we do, although our
studies cannot be directly compared with each other. While their approach has several
similarities with our BAE analysis, our population is different from theirs in that it
includes all adult heirs (not only children). The key difference, however, is that our
data contain information about the value of their inheritances, which allows us to
estimate the direct mechanical effect and dig deeper into how and why inheritances affect
wealth inequality and mobility. It also allows us to study how inheritance taxation
affects wealth inequality.6 The remainder of the paper is structured as follows. Section 2
presents the institutional context and the data. Section 3 presents our main findings.
Section 4 explains how wealth mobility is influenced by inheritances, and Section 5
discusses the role of inheritance taxation. Section 6 discusses some implications of our
findings.

<h>INSTITUTIONAL CONTEXT AND DATA</h>
------------------------------

In this section, we present the Swedish legislation regarding inheritances and inheritance
taxation. Moreover, we provide descriptions of the data and the study population and
discuss the various measures of wealth inequality that we use in the empirical analysis.

<hs>  Inheritance legislation and taxation</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In Sweden, when a person passes away, an estate inventory report should be filed with the
tax agency, reporting the values of the decedent's assets and debts. If the decedent has a
positive net worth, his or her estate is distributed to the heirs according to a
succession scheme that is based on genetic relationships. The decedent's relatives are
classified into three groups of legal heirs: children and their offspring, parents and
their offspring (the decedent's siblings, nephews and nieces), and grandparents and their
children (i.e., aunts and uncles).7 Heirs in the second (third) group inherit only if
there are no heirs in first (first or second) group. If the decedent has a spouse, the
estate is transferred to him or her. If the spouses have common children, the surviving
spouse receives what is referred to as free disposal of the estate, which means that the
money could be spent but not bequeathed to others than the children. The common children
receive the inheritance from the first deceased parent when the second parent passes away.
The deceased's children who are not common with the surviving spouse will, on the other,
hand inherit immediately when their parent passes away. The default succession scheme can
be set aside by a will, but children are always entitled to half of what they would
inherit in the case of intestacy, i.e., in the absence of a will. It should be noted also
that heirs do not inherit any debts that the decedents may have at the time of death.
Inheritance and gift taxes existed in Sweden until their abolishment by the end of 2004.8
In the early 2000s, inheritances exceeding SEK 70,000 (approximately USD 11,000)9 were
taxed according to a progressive three-bracket schedule, with marginal tax rates ranging
from 10% (paid by heirs who inherited amounts approximately between the 70th and the 90th
percentiles in the inheritance distribution) to 30% in the highest bracket on inheritances
over SEK 600,000 (USD 91,000, paid by, approximately, the top 2%).10 All inherited assets
were taxable, but important concessions were made to keep the effective tax down on
certain assets, especially firm equity (see also Ohlsson, 2011 and Henrekson and
Waldenström, 2016).

<hs>  Data and study population</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~

Our main data source is a population-wide register called Belinda. It originates from the
Swedish Tax Agency and contains detailed accounts of the estates of, and inheritances,
from all individuals who passed away in 2002–2004 and all of their biological and non-
biological heirs. Data are available from this period because the tax agency was obliged
to electronically codify all estate reports starting in July 2001, but this obligation was
suspended in 2005 when the inheritance tax had been abolished. To these data, we have
added information from other administrative registers, primarily those covering personal
wealth but also other relevant economic and demographic characteristics for both the
decedents and their heirs. In particular, the information about decedents in Belinda
includes the net worth at death and its main components (total assets and total debts),
the value of the estate, a list of heirs, special rules that apply to the estate and the
bequests (e.g., will, prenuptial agreement, and life insurance policy) and personal
details (e.g., identity number, marital status, and death date). The information about
heirs in Belinda includes the value of their received inheritance, inheritance tax
payments (if any), the taxable gifts received over the past ten years, the receipt of life
insurance payments from the deceased and personal details (e.g., identity number and
relationship to the decedent). Inheritances from a previous decedent (e.g., a late
spouse), which the current decedent possessed with free disposal, are divided between the
previous decedent's heirs, and the amounts are listed separately in the database. We
define inheritance as the total net-of-tax value of inheritances and any insurance
received from the decedent (unless it is explicitly stated to be the before-tax
inheritance). For heirs who receive two inheritances when the decedent passes away
(typically a child who receives one inheritance from the recently deceased parent and one
from a previously deceased parent), we define the inheritance as the total sum of these
transfers (plus any insurance payments from the two decedents, net of tax). It should be
noted that the estates and inheritances observed in the data are reported at tax values,
which are sometimes lower than the market values. For instance, real estate was valued at
the tax-assessed value, intended to correspond to approximately 75% of the market value.
In the main analyses, we use the amounts as given in the database but, in robustness
tests, we investigate how the results change when we attempt to adjust the inheritance
values to their market values. We define heirs as individuals who live in Sweden and
receive an inheritance through the succession order, are beneficiaries of a will, or are
beneficiaries of a life insurance policy. We focus on the final estate division of a
household and, therefore, do not include heirs who were the spouse or partner of the
decedent in our study population. We further restrict our attention to heirs who were at
least 18 years old in the year when the decedent passed away because inheritances received
by minors fall under the protection of a guardian and are, in practice, controlled by the
parents.11 A key feature of our analysis is our classification of heirs into inheritance
cohorts according to the year when the deceased passed away. We thus have three
inheritance cohorts: 2002, 2003 and 2004, covering a total of 475,120 heirs connected to
168,055 decedents. Wealth data are collected from the wealth register of Statistics
Sweden, which is available for the 1999–2007 period, i.e., several years before and after
the 2002–2004 inheritance years. The wealth register contains detailed accounts of real
and financial assets and debts, all recorded in market values at each year's end, for all
individuals in the population. We focus on private net worth, which is the market value of
real and financial assets less all debts. Specifically, on the asset side, the wealth
portfolios comprise non-financial assets (owner-occupied housing, secondary homes, land,
agricultural property, commercial real estate, etc.) and financial assets (bank deposits,
listed stocks and bonds, mutual funds and other financial securities). Debts are mainly
mortgage loans and state-subsidized loans for higher education. The wealth data are
particularly advantageous because the bulk of the records come from third-party reports to
the tax agency by financial institutions. The wealth register has limited information
about some assets. The register does not cover funded pension assets. In addition, closely
held corporations are incompletely covered, and compared with estimates of their aggregate
value reported in the Financial Accounts, only about one tenth is accounted for in the
wealth register. While these limitations are unfortunate, even when these assets are
observed, e.g., in surveys, they are notoriously difficult to value and are, moreover, not
always fully marketable. Moreover, consumer durables are not well covered by the wealth
register. This may be problematic for an analysis of distributional consequences of
inheritances since these goods can be important, not least in relative terms in less
wealthy households.12 In the robustness analyses we, therefore, attempt to assess how
sensitive our results are to the undervaluation of consumer durables by approximating the
value of these goods using, e.g., estimated car values. Despite some shortcomings, it
should be noted that our wealth data are the same ones as those used in the international
wealth data project, the Luxemburg Wealth Study (see Sierminska et al., 2006).

<hs>  Descriptive statistics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

This study offers the first comprehensive view of the distribution of estates and
inheritances in a population-wide register (see Fig. 1).13 First, we observe that the
distribution of the decedents' estates is highly skewed, as most of the mass is located in
the left tail and 17% of the estates have zero value. The median value is just over SEK
93,000 (approximately USD 14,000), the mean is approximately SEK 264,000 (USD 40,000) and
the 99th percentile of estates is approximately SEK 2.2 million (USD 330,000). The top
percentile share accounts for 19% of the total estate wealth, and the top decile accounts
for 55%, which are levels that are consistent with those of previous wealth distribution
studies (Roine and Waldenström, 2009). Second, the distribution of the inheritances that
the heirs receive is similar to that of the estates—skewed, with 19% of the heirs
inheriting nothing at all; the top tenth of inheritances represent 56% of the total
inherited wealth. Third, the graph in the lower left-hand corner displays the wealth
distributions in the year before inheritance (T − 1) for each inheritance cohort. These
distributions are nearly identical across the cohorts, highly skewed (with Gini
coefficients of approximately 0.8, as examined further in the next section) and show that
a non-negligible fraction of the heirs have zero14 or close to zero wealth. Finally, the
figure displays the heirs' age distribution. A slight majority of the heirs (56%) are
between 50 and 70 years old. Table 1 presents additional descriptive statistics. The
inheritance cohorts are nearly identical in all dimensions, which is also expected, as
they comprise essentially the entire population of inheriting individuals for each year.15
The average wealth of the heirs one year prior to the inheritance year varies somewhat
across cohorts. This variation likely reflects annual differences in macroeconomic
conditions, particularly stock market and housing price changes. The bottom panel of the
table shows statistics for the decedents. Similar to the statistics for the heirs, the
differences are very small, and we thus conclude that the inheritance cohorts are also
similar in terms of the characteristics of the donors.

<hs>  Measuring wealth inequality</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~

The measurement of wealth inequality is somewhat more complex than the measurement of, for
instance, income inequality because some individuals have negative wealth (i.e., when
debts are larger than assets). Therefore, we conduct our analyses using various
unidimensional inequality measures that are defined for variables containing positive as
well as negative values.16 Our focus is on the Gini coefficient, which is the most widely
used inequality measure. While the statistical properties of the Gini coefficient are
fully intact when negative values exist, the normative interpretations from a certain
level or trend may be less straightforward (e.g., How should the negative shares of a pie
be distributed?). We complement the analysis with other unidimensional inequality measures
that can handle negative values: top and bottom wealth shares, wealth percentile ratios,
and a measure of absolute dispersion (the interquartile wealth range, and, in the Online
Appendix, also the range between the 1st and 99th wealth percentiles, as well as the
coefficient of variation).

<h>THE EFFECT OF INHERITING ON WEALTH INEQUALITY</h>
---------------------------------------------

We estimate two types of inheritance effects on wealth inequality among heirs: one direct
mechanical and one behavior-adjusted. Conceptually, the direct mechanical effect (DME)
represents the immediate distributional change that arises from adding the inherited
amount to the heirs' pre-inheritance wealth. This is our main estimator of interest as it
offers the clearest channel from inheritance to inequality change. The behavior-adjusted
effect (BAE) accounts for behavioral responses among heirs, which reflect that receiving
an inheritance may influence labor supply, consumption and investment decisions that, in
turn, may affect wealth accumulation and inequality. The estimations of the two effects
are performed both non-parametrically, showing how the distribution changes graphically,
and for the different unidimensional measures of inequality. We focus on heirs of all the
decedents who passed away between 2002 and 2004. Focusing on heirs is a natural starting
point for our study of the distributional consequences of inheritances because almost
everyone inherits sooner or later in life, whether the inheritance is a tiny amount (or
even zero) or a larger sum.

<hs>  The direct mechanical inheritance effect</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The DME captures how the wealth distribution among the heirs will change if the heirs save
their entire inheritances and nothing else happens. To evaluate this effect, we would like
to compare the inequality in the wealth distribution in the period just before the heirs
inherit to the inequality in the distribution in the period just after the inheritance.
Denoting the measure of the wealth distribution of interest DW (e.g., the Gini
coefficient), the time of the inheritance T and the length of time until the inheritance
ε, the DME on DW would be given by DT+εW − DT−εW. To estimate the DME using this strategy,
ε would need to be extremely small (e.g., one day) to avoid the influence of behavioral
responses. However, we do not know the exact date when heirs received their inheritances
(only the date when the decedents passed away), and we only observe their wealth on
December 31 of each year. Comparing wealth distributions in the years before and after
inheritance is clearly a too long time span to identify the DME because behavioral
responses and changes in macroeconomic conditions may confound the estimates. To examine
the statistical robustness of the effect, we compute standard errors by bootstrapping the
estimates using 1000 repetitions. The standard errors are typically very small, reflecting
both that the DMEs are mechanical in nature, without any stochastic element, and the large
size of the dataset.

        Estimation results: direct mechanical effect

        We start by presenting a non-parametric estimation of the DME, which evaluates how
        the density distribution of wealth changes as a consequence of inheritances. Fig.
        2 shows how the wealth distribution changes at different wealth levels when we add
        each heir's inheritance to his or her pre-inheritance wealth. Clearly, a
        pronounced drop in density occurs around zero wealth, and a sizable increase in
        density occurs at moderate wealth levels. Thus, heirs with zero (or almost zero)
        wealth move up in the distribution after having received inheritances. By
        contrast, no changes appear at very low (negative) and very high wealth levels. In
        these segments, the densities are similar both before and after inheritance, and
        the differences in the graph are accordingly quite close to the zero line. In
        other words, adding inheritances to the heirs' pre-inheritance wealth has the
        largest influence, quantitatively, on the middle parts of the wealth distribution,
        whereas the tails are nearly unaffected. We now shift focus to estimate the DME on
        unidimensional measures of wealth inequality. We seek to quantify the
        distributional effects of inheritance in terms of standard measures of inequality,
        which, in turn, facilitates comparisons with other factors and events that affect
        the wealth distribution. Panel A of Table 2 presents the DME on five
        unidimensional measures of inequality that were discussed in Section 2.4.17 The
        estimated effects with respect to these measures mirror the pattern displayed in
        Fig. 2. First, we see that the relative inequality decreases. The Gini coefficient
        falls from 0.804 to 0.748 (averaged over the three inheritance cohorts),
        corresponding to a reduction of 7% - a substantial equalization effect. For
        example, this drop in the Gini coefficient is larger than that following the
        dotcom bubble in 2000, when stock prices fell sharply, affecting primarily
        stockholders (who are typically in the top of the distribution). Similar results,
        showing an equalizing effect, are found for the other measures of relative
        inequality. The wealth percentile ratio P90/P50 falls quite substantially—by
        approximately 17%. The wealth share of the top decile also falls, from 55.9 to
        52.3% (a 7% drop), while the wealth share of the bottom half of the distribution
        actually increases from minus 1.5% to plus 2%. Interestingly, the measure of
        absolute dispersion, the wealth percentile gap P75–P25, increases by 8%, which
        confirms the pattern of a high correlation of wealth across generations, in
        general, and between the heirs' wealth and inheritance amounts in particular. In
        summary, the results with respect to the DME indicate that inheritances equalize
        the wealth distribution of heirs, an effect that is consistent across both non-
        parametric estimation of the change in distribution and a range of well-known
        wealth inequality measures. In addition, the data confirm the conventionally held
        view that richer heirs inherit more than poorer heirs do, as indicated by the
        increased absolute dispersion of wealth. Our results so far show the effect of
        inheritances on the wealth distribution among all heirs, not only the children of
        the decedents. To facilitate comparisons with previous studies focusing on
        children heirs, and to rule out the possibility that our results are driven by
        including all family and non-family heirs, panel B of Table 2 presents the DME
        estimates for a sample consisting only of the decedents' children. The point
        estimates indicate a slightly larger equalizing effect of inheritances and a
        larger increase in the absolute dispersion among the children-heirs, but the
        differences between the two samples are small. We, thus, conclude that the choice
        of including or excluding heirs other than the children of the decedents is not
        important for our main conclusion that inheritances decrease relative inequality
        and increase absolute dispersion. In Table 3, we present results from several
        additional robustness tests. We show that the equalizing effects are more
        pronounced among the younger (and less wealthy) heirs, but still important across
        all ages and that our results are robust to the inclusion of heirs younger than 18
        years, at the time of the inheritance (see panels A and B, and Online Appendix
        B.2.1 for details).18 Moreover, we perform several tests intended to assess how
        sensitive our results are to alternative measurements of wealth and inheritance
        measures. These tests show first, that the underreporting of consumer durables in
        our main wealth measures and, second, that using inheritances at market values
        (rather than at tax values as recorded in the data), have a minimal impact on our
        results (see panels C–E, and Online Appendices B.2.2 and B.2.3 for details).
        Finally, we dig deeper into how inheritance of financial and real assets affect
        inequality in the distributions of financial and real assets (see panels F and G,
        and Online Appendix B.2.4 for details). Since financial assets are more liquid
        than real assets, inheritances containing more real estate will affect consumption
        possibilities in the short run less than inheritances containing more financial
        assets. We find that inheritances reduce inequality in both financial and real
        estate assets, but that the effect is more pronounced for financial assets. This
        follows, as we show in Fig. B1, from the fact that inheritances typically contain
        equal amounts of real and financial assets and that a large fraction of heirs own
        real estate while only relatively few (but rich) had substantial amounts in
        financial assets.

        How can the equalizing effect be explained?

        The result that inheritances lead to lower relative wealth inequality is explained
        by the distribution of inheritances being more equal than the distribution of
        wealth among the heirs. If the distribution of wealth of decedents is more equal
        than the distribution of wealth among heirs and all decedents split their wealth
        equally between their children and have the same number of children, then the
        distribution of inheritances will also be more equal than the distribution of
        wealth among the heirs. These conditions appear to be met in our data. The Gini
        coefficient for the distribution of wealth among the decedents (in the year before
        the demise) is 0.76 and the Gini coefficient for the distribution of inheritances
        (net of taxes) is 0.73, while the Gini of the wealth distribution among the heirs
        (in the year before inheriting) is 0.80. Because wealth is positively correlated
        across generations (see, e.g., Charles and Hurst, 2003),19 wealthier heirs receive
        larger inheritances in absolute amounts, but because the distribution of
        inheritances is more equal than the distribution of wealth among heirs, less
        wealthy heirs will inherit more relative to the wealth they already hold prior to
        receiving the inheritance. Fig. 3 shows how the inherited amounts vary with the
        wealth of heirs. Looking first at absolute amounts (right axis), we see that
        wealthier heirs inherit more money.20 For example, heirs in the fourth wealth
        decile (ranked before inheriting) receive inheritances worth, on average, SEK
        64,000, whereas heirs in the top decile inherited, on average, SEK 193,000. Thus,
        there is a positive association between the heirs' wealth and the amount
        inherited, which explains why absolute dispersion increases. When looking at the
        relative importance of inheritances instead, dividing inheritances by the heirs'
        wealth, the pattern is reversed. Heirs in the fourth wealth decile receive
        inheritances that are larger than their own wealth, whereas heirs in the top
        decile receive inheritances worth only one twentieth of their wealth. This pattern
        explains the decrease in relative wealth inequality among heirs. Relatively poor
        heirs often inherit amounts that are large relative to their own wealth, while
        this is typically not the case for richer heirs. The equalizing effect can be
        explained solely by the distribution of wealth among the decedents being more
        equal than the distribution of wealth among the heirs. Any factor affecting wealth
        accumulation processes among the donor generation and the heir generation may thus
        affect how inheritances affect the wealth distribution among heirs.21 Still,
        inheritances appears to be more equally distributed than the wealth of the
        decedents, which then contributes to the equalizing effect we find. Several
        mechanisms may be responsible for why the distribution of inheritances is more
        equal than the distribution of wealth among the decedents. Below, we address the
        importance of five such mechanisms. First, if wealthier decedents have more
        children, their estates will be distributed among more lots, causing each child to
        inherit less than he or she would have done had there been fewer children.22
        However, we find no support for this mechanism. In particular, richer decedents do
        not have more children than less wealthy decedents and variation in the number of
        children has no important impact on the results. See panel A in Table 4, and
        Online Appendix B.3.1 for details. Second, if wealthier decedents testate a
        disproportionally larger share of their wealth to charities, the heirs would
        inherit less than they would have done in the absence of charitable bequests. In
        our data, we see that wealthier decedents indeed testate a larger fraction of
        their estate to charities. This in line with the literature on charitable
        contributions at death (see, e.g., Joulfaian, 2001).23 However, even among the
        wealthiest decedents, only 2.5% of the estate goes to charity. Moreover, a
        counterfactual analysis, in which we redistribute the charitable bequests to the
        heirs, produces DMEs that are essentially identical to the main ones. We are
        therefore confident that charitable bequests among the rich are not the driver
        behind the finding that inheritances lead to lower relative inequality. See panel
        B in Table 4, and Online Appendix B.3.2 for details. Third, if wealthier decedents
        circumvent the default succession rules by writing wills stating that part of
        their wealth should go to individuals outside the succession order, each heir
        would inherit less than he or she would have done in the case of intestacy. We
        address the relevance of this mechanism by calculating the hypothetical
        inheritance each child would receive in the absence of wills. The DMEs from this
        counterfactual exercise are largely similar to the main results, suggesting that
        the equalizing effect cannot be explained by richer decedents' preferences for
        distributing their wealth among more heirs. The results also suggest that the
        limited freedom to testate in the Swedish and Roman inheritance law tradition
        (Pestieau, 2003) is not the driver of the equalizing effect. See panel C in Table
        4, and Online Appendix B.3.3 for details. Fourth, intergenerational transfers
        consist of both inheritances at death and gifts that the decedents give to their
        heirs during their lifetime, i.e., inter vivos. If substantial amounts were
        transferred during the years just prior to the inheritance, the interpretation of
        our results could be misleading. If richer parents were more likely to transfer
        wealth to their children in the years before the demise, the DMEs would show more
        equalization than if these transfers would instead take place as inheritances. We
        conduct several tests, using both data on reported taxable gifts and by assuming
        that the gift giving patterns in our sample are similar to those in other data
        sources (Ohlsson et al., 2014; Piketty and Zucman, 2015). We find that decedents
        with smaller estates make smaller gifts in absolute terms, but that they give away
        larger shares of their wealth. If we add the value of gifts to the inherited
        amounts, we find slightly larger equalizing effects. This suggests that the
        equalizing effects are not much affected by inter vivos gifts. See panels D–G in
        Table 4, and Online Appendix B.3.4 for details. Fifth, the inheritance law states
        that the heirs do not inherit the decedent's debts. If the decedent has negative
        net wealth, the heirs will inherit zero. This feature of the inheritance law makes
        the inheritance distribution more equal than the wealth distribution of the
        decedents. If we replace all negative wealth values with zeros and calculate the
        Gini coefficient for the wealth distribution of the decedents (in the year before
        the demise), we obtain a value of 0.73, which is akin to the Gini for the
        inheritance distribution but lower than the Gini for decedent wealth including
        negative values, which is 0.76. It is hence clear that this part of the
        inheritance law contributes to the equalizing effects that we find. Out of the
        five mechanisms discussed above, only the last one appears to be quantitatively
        important. Another possible explanation for the result is methodological and
        concerns the identification strategy. If heirs have adjusted their savings in the
        years prior to inheritance because they expect to receive inheritances,
        potentially important parts of the total wealth response to inheritances may be
        overlooked with the strategy. Heirs expecting large inheritances are likely to
        save less than heirs expecting a small inheritance. As such, the pre-inheritance
        wealth distribution will be more compressed than in a world in which heirs do not
        adjust savings decisions based on their inheritance-related expectations.
        Consequently, the total effect of inheritances—including both pre-inheritance and
        post-inheritance responses—might be more equalizing than what our estimates
        suggest. Quantifying expectation responses to inheritances is difficult, and only
        a few studies have attempted to do so (Wolff, 2015; Elinder et al., 2012).24 We
        conduct tests designed to assess how expectations about future inheritances may
        influence heirs' pre-inheritance wealth levels. A first test is based on the idea
        that if decedents (in the years before the demise) suddenly become richer (poorer)
        and heirs adjust their savings in response to changes in the expected size of
        inheritances, we expect that the heirs will respond by dissaving (saving) an
        offsetting amount of wealth. In a second test, we exploit the idea that heirs may
        respond more strongly to changes in the decedent's wealth in the years before
        inheritance if the decedent passes away as a result of a terminal illness rather
        than passing away suddenly. To investigate this idea more carefully, we use data
        from the Cause of Death register to identify heir-decedent pairs in which the
        decedent has passed away suddenly. The classification of sudden deaths (natural
        and unnatural) follows the classification in Andersen and Nielsen (2011). Neither
        of the tests provide evidence of responses in the heirs' wealth prior to
        inheritance. Altogether, the concern that heirs' saving behaviors depend on their
        inheritance expectations may be plausible, but we find little evidence in our
        data—or in the previous literature—that these behaviors will confound our main
        findings. While we clearly cannot rule out that such behavioral effects exist,
        they do not seem to matter much empirically. See Online Appendix B.3.5 for
        details.

<hs>  The behavior-adjusted inheritance effect</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

When empirically estimating the BAE on wealth inequality (and mobility), several
challenges arise related to concerns about the ceteris paribus condition not being
fulfilled. To illustrate the two most prominent challenges, consider first a strategy that
compares the wealth distribution of heirs before and after the receipt of inheritance. The
difference between the two distributions may be caused by inheriting only, though a
singular source is unlikely. For example, macroeconomic events, such as housing market
downturns, tend to slash middle-class wealth and thus increase wealth inequality, whereas
financial market crashes primarily hit the wealthy and tend to make the wealth
distribution more equal (Wolff, 2013; Lundberg and Waldenström, 2018). Second, age-wealth
profiles generally imply that, within a birth cohort, wealth becomes more equally
distributed with age (Paglin, 1975). Therefore, a simple before-after analysis may yield
biased estimates of the effects of inheritances on the wealth distribution. In Eq. (3),
Dc, yW denotes the wealth inequality that varies across cohort c and calendar year y.
PostInheritance is a cohort-specific indicator variable, which equals one from the year of
the inheritance and onwards. We also include year and cohort fixed effects, captured by λy
and λc, respectively, and εc, y is a random error term. The estimation model is
essentially a difference-in-differences estimator, where the identifying assumption is
that the outcome would have evolved similarly for the inheriting cohort and the “to-
inherit” cohort(s) in the absence of inheritance (i.e., a parallel trends assumption).
While this assumption cannot be explicitly tested, it is possible to obtain indirect
evidence of whether it holds by studying the outcome trends for the groups in the pre-
treatment period, i.e., before inheritance. In the next section, we investigate the
validity of the assumption and show that it appears to hold.

        Estimation results: behavior-adjusted effect

        Similar to the DME analysis, we start the BAE analysis with a non-parametrical,
        graphical illustration. The estimated effect of inheritance, by comparing pre- and
        post-distributions, may be biased by macroeconomic and demographic (aging)
        influences; to account for such potential confounders, we compare the wealth
        distribution changes of the 2002 and 2004 inheritance cohorts between 2001 and
        2003, i.e., when the 2002 cohort inherits, and the 2004 cohort does not. Because
        both cohorts experience the same macro environment and aging process, the
        differences in wealth distributions effectively only reflect the inheritances of
        the 2002 cohort.26 Fig. 4 shows the results. An initial observation is that the
        pattern resembles the one seen for the DME in Fig. 2 (and reproduced here: dashed
        line in grey); inheritances positively affect a substantial mass of heirs from the
        bottom and the middle of the distribution. That said, the size of the BAE is
        apparently smaller than the DME. Next, we turn to analyzing the BAE on
        unidimensional wealth inequality and absolute dispersion. In contrast to the
        graphical analysis, we now use the 2002, 2003 and 2004 cohorts simultaneously and
        exploit the full wealth register data from 1999 to 2007. Therefore, the estimated
        inheritance effect can capture the average effect up to five years after
        inheritance, but in practice, most of the variation used in the estimations of the
        effect comes from the first two years after inheriting, which is why it is safer
        to say that we capture the effect up to two years after inheriting. As noted in
        the previous section, the identification strategy assumes that wealth inequality
        would evolve similarly for all cohorts had they not inherited. Fig. 5 depicts the
        evolution of the Gini coefficient for the three cohorts over the entire period.
        Until 2001, i.e., the year before the first cohort inherits, a near-identical
        development of the Gini coefficient occurs for all three cohorts, strongly
        suggesting that the parallel trends assumption is fulfilled. The Gini coefficients
        fall from approximately 0.85 in 1999 to 0.82 in 2000 and 0.81 in 2001. In 2002,
        the 2002 cohort inherits, and we see an immediate and sharp drop in the Gini
        coefficient to 0.78, falling further in 2003 when the heirs of the decedents who
        passed away in late 2002 received their inheritances. By contrast, the Gini
        coefficients of the two non-inheriting cohorts remain virtually unchanged in 2002.
        Starting in 2003, when the 2003 cohort inherits, the Gini coefficients of that
        cohort drop over the next two years. This pattern is repeated again for the 2004
        cohort. Between 2005 and 2007, when all the cohorts have inherited, the Gini
        coefficients return to a common level and development. As clearly shown in Fig. 5,
        changes in wealth inequality differ across the cohorts only in the two years when
        they inherit. This strikingly consistent pattern offers strong evidence that the
        equalizing effect of inheritances on the wealth distribution persist for at least
        a few years. Table 5 reports the estimation results of the BAE on the five
        inequality and dispersion measures generated by the difference-in-differences
        estimator (Eq. (3)). The coefficient estimate in the first column shows that the
        inheritance effect causes a reduction in the Gini coefficient by 0.037 points,
        which is equivalent to a drop of 4.6% (when compared with the baseline of 0.804).
        In Online Appendix B.4.2, Table B5, we show that the BAEs are robust in the
        dimensions as the DMEs. The estimates of the inheritance effects on the other
        relative dispersion measures confirm what we have observed already in Figs. 4 and
        5, and they are qualitatively similar to the DMEs. The P90/P50 decreases by 10.5%,
        and the share of total wealth held by the wealthiest decile falls by 5%. Notably,
        the poorest half increases their share of total wealth from minus 1.6% to just
        above zero. Finally, the estimated effect of inheritances on the distance between
        the 75th and the 25thh wealth percentiles indicates that wealth dispersion
        increases as a consequence of inheritances. Taken together, the results confirm
        the patterns we found when we estimated the DME, which was that relative
        inequality decreases while absolute dispersion increases, suggesting that
        behavioral responses to inheritances do not mute the equalization effect, at least
        not in the short-run. To be able to firmly assess whether the equalizing effect
        remains in a longer perspective, we would need more inheritance cohorts that
        inherit in later years and could serve as longer-run counterfactuals for the
        cohorts who inherit early. In Online Appendix B.4.3 Fig. B6, we use a slightly
        different dataset in an attempt to investigate whether the equalizing effects are
        still present five years after inheriting. The results suggest that the equalizing
        effect is present at least up to five years after inheriting. Unfortunately, data
        restrictions imply that we cannot say whether the effect decreases or increases
        over a period of more than five years. That said, the equalizing effects appear to
        be smaller when accounting for the behavioral adjustments of the wealth holdings.
        Therefore, we continue by investigating some possible explanations for this
        finding in the next section.

        Potential explanations for why is the behavior-adjusted effect is smaller than the direct mechanical effect?

        When comparing the two inheritance effects on wealth inequality, we see that the
        BAE is smaller than the DME. In the case of Gini coefficients, the BAE is 5%, and
        the DME is 7%. We discuss two possibilities for this discrepancy. The first
        relates to behavioral responses among the heirs, which may dilute the equalizing
        effect. The second relates to methodological differences between the DME and BAE.
        The task to separate the relative importance of the two explanations is, however,
        beyond the scope of this paper. Why might the equalizing effect of inheritances be
        less pronounced when behavioral responses are accounted for? Departing from a
        standard framework for wealth accumulation, several possible explanations are
        consistent with such a pattern.27 Compared with wealthier heirs, less wealthy
        heirs have a higher marginal propensity to consume their inheritances (see, e.g.,
        Druedahl and Martinello, 2017). The second explanation is that wealthier heirs
        receive higher returns on their savings than poorer heirs do (Andersen and
        Nielsen, 2011). Both of these explanations would lead to increased wealth
        inequality and, in turn, mitigate the equalizing direct mechanical effect.28
        However, without data on consumption, we cannot credibly assess the importance of
        these two explanations for our findings. The difference between the DMEs and the
        BAEs could potentially also result from differences in the estimation methods. A
        key difference between the two estimation methods is that the DME uses wealth data
        in the year before inheriting and data on the inheritance, while the estimation of
        BME is based only on wealth data, but for several years. A potential concern here
        is discrepancies between how wealth and inheritances are measured. While the
        wealth data are recorded at market values, the data essentially lack consumer
        durables. The inheritances, on the other hand, include durables but are recorded
        at tax values. As discussed in Section 2.4, for some asset types, most notably
        stocks and real estate, the tax value is lower than the market value. However, in
        Online Appendices B.2.2 and B.4.2, we show that the DMEs and the BAEs are not
        altered much when we attempt to correct for the underreporting of consumer
        durables. Moreover, in Online Appendix B.2.3, we showed that the DMEs are not
        altered when we attempt to adjust inheritances to market values. We, therefore,
        find no indications that the differences in the DMEs and BAEs stem from these
        types of measurement errors. However, we cannot rule out that the differences
        between the DMEs and BAEs are the result of any difference in how the effects are
        estimated.

<h>INHERITANCE AND WEALTH MOBILITY</h>
-------------------------------

Another possible consequence of the effects of intergenerational transfers is that they
may influence the level of wealth mobility among the heirs. We are interested in mobility
effects for two reasons. First, the normative interpretation of the inequality effects
depends on how mobility is affected. Inheritances decrease relative inequality, but do
inheritances also increase the chances of the poor to increase their wealth rank? Second,
do inheritances set off mobility processes? If receiving inheritances makes people behave
differently, perhaps taking more risk or changing their activity in the labor market,
inheritances may affect wealth mobility long after the receipt. Even though our previous
analysis indicated that behavioral effects exist, mainly working to mute the
distributional consequences, perhaps the effect on mobility will still be more evident in
this respect? This section presents an analysis—to the best of our knowledge, the first of
its kind—on how inheritances influence wealth mobility. Our focus is on intragenerational
wealth mobility, which means the rate at which heirs change wealth ranks in their
distribution.29 There are several different ways to empirically measure intragenerational
wealth mobility as discussed by Burkhauser and Couch (2009) and Jäntti and Jenkins (2015).
We show results using one of the most common methods, which involves calculating
transition probability matrices in the wealth distribution for heirs before and after
inheritance. By comparing transition probabilities across quintiles, the matrix shows
whether actual mobility patterns at the bottom, the middle and the top of the distribution
differ. We then convert these matrices into a unidimensional metric, the Shorrocks-Prais
mobility index (Prais, 1955; Shorrocks, 1978), which is an index centered on the diagonal
elements in the matrices and ranges from 0 (perfect immobility) to 1 (perfect mobility).30
For robustness purposes, we also examine the change in Spearman rank correlation
coefficients between the same distributions, i.e., heirs' wealth before and after
receiving an inheritance. While the difference in Spearman correlations is not a direct
measure of mobility, it imposes less structure and relies on fewer assumptions than the
Shorrocks-Prais index. The DME for mobility is estimated by computing two transition
matrices, one measuring the individual transitions from T − 2 to T − 1 (with the
inheritance) and the mobility measure for the transition period from T − 2 to T − 1
(without the inheritance). Table 6 shows that the Shorrocks-Prais index increases by 43%
when adding inheritances, which means that mobility increases substantially as a result of
inheriting. When evaluating leaving probabilities across wealth quintiles (columns 2
through 6), we see that the mobility effect is larger among heirs in the lower part of the
wealth distribution than among the heirs in the top. As a sign of robustness of this
effect, the last column of the table shows that inheriting wealth also leads to a
significant decrease in the rate of change in Spearman rank correlations across years.
Such a decrease reflects a higher degree of rank movements along the wealth distribution
when inheriting, which is in line with higher intragenerational mobility. We also estimate
the DME on mobility for the Children sample. The results, reported in Online Appendix
B.5.2, display a similar pattern to those for the full sample. To estimate the BAE for
mobility, we implement the same approach as in the inequality analysis. In Fig. 6, we
depict the evolution of Shorrocks-Prais mobility indices for wealth transitions around the
year of inheritance (i.e., from Wpre to Wpost). The parallel trends assumption appears to
hold, judging from the similar levels of wealth mobility in the pre-inheritance transition
periods. Despite an overall rise in mobility from 2001 to 2002, the 2002 inheritance
cohort exhibits an even higher mobility increase, from 0.23 to 0.32, than the two other
cohorts (which increase from 0.23 to 0.28). One year later, the 2003 cohort experiences a
similarly large mobility increase, and, another year later, the 2004 cohort experiences
the same relatively large increase in mobility (the mobility increase is marginal in
absolute terms, but, because the other two cohorts experience substantial decreases in the
same period, the effect can be stated as a relative increase). To be more precise in
determining the magnitude of the BAE, we estimate the effect using the difference-in-
differences model of Eq. (3).31 The results in Table 7 show that overall mobility
increases by 19% (a treatment effect of 0.048 compared with the average pre-inheritance
Shorrocks-Prais index of 0.260). Although significant, this effect is less than half the
DME reported in Table 6. When examining leaving probabilities across wealth quintiles
(columns 2–6), almost no difference in mobility is found across the distribution, with
mobility increases between 13 and 21% depending on the part of the distribution that is
considered. The change in Spearman rank correlations exhibits once again a similar pattern
as the mobility index, showing a decrease in correlation in the periods after inheritances
are received, and the effect is also smaller than in the DME analysis. We also estimate
the BAE on mobility for the Children sample. The results, reported in Online Appendix
B.5.2, display a similar pattern to those for the full sample. In Online Appendix B.5.3,
we attempt to see whether the mobility effect is persistent up to five years after
inheriting. That analysis suggests, however, that the mobility effect is short-lived; it
seems to last only two to three years. Two important messages emanate from the mobility
analysis presented here. The first is that inheritances substantially increase wealth
mobility. In particular, many of the heirs who were among the poorest before inheriting
rise in wealth rank. The second message is that inheritances set off increased mobility in
the first years after inheriting, but that effect does not seem to be persistent in the
longer run.

<h>INHERITANCE TAXATION AND WEALTH INEQUALITY</h>
------------------------------------------

In this section, we present the first empirical analysis of inheritance taxation on wealth
inequality using individual-level register data.32 The distributional consequences of
taxation on intergenerational transfers have received relatively little attention in the
previous literature. Theoretical models that address this issue implement diverse
analytical approaches, but most of them predict that inheritance (or estate) taxes
increase wealth inequality (e.g., Stiglitz, 1978; Becker and Tomes, 1979; Atkinson, 1980;
Davies, 1986).33 While these models typically focus on general equilibrium and long-term
consequences of inheritance taxation, our analysis instead examines short-term
consequences that are associated with the repeal of Sweden's inheritance tax. We begin by
examining how the DMEs change due to the tax payments by the heirs. To estimate the effect
of the tax, we calculate the difference between the DMEs using inheritances net-of-
inheritance-tax payments (as in Table 2) and DMEs using inheritances before tax payments.
The estimated effects are economically relevant as the repeal was effectively unexpected,
announced just a few months before the repeal actually occurred. However, it should be
noted that our analysis is limited by being mechanical and short-term. It does not account
for any behavioral adjustments to inheritance taxation that donors or heirs may make over
the longer run. The results are reported in Table 8 and should be interpreted as the
effect of a repeal of the inheritance tax on wealth inequality. The tax repeal effect
suggests that the inheritance tax increases relative inequality but decreases absolute
dispersion. However, the magnitudes of these effects are very small. For example, the Gini
coefficient falls by an additional 0.002 points due to the tax repeal. This relatively
small effect is reasonable, given the rather small amounts of inheritance and gift tax
payments in the early 2000s. To explain what causes the disequalizing effect of the
inheritance tax, Fig. 7 displays the average level of inheritance and gift tax payments by
the heirs' pre-inheritance wealth levels. Wealthier heirs pay more in taxes in absolute
terms but less relative to their initial wealth. This finding implies that, for the
wealthiest heirs, both their inheritances and inheritance taxes are relatively
insignificant in relation to their pre-inheritance wealth, while both inheritances and tax
payments are substantial relative to the pre-inheritance wealth of the less wealthy. We
thus interpret the results of the test as evidence that the equalizing effect of
inheritances would have been slightly stronger without the inheritance tax. The analysis
has hitherto only considered the tax payments and not the possible uses of the tax
revenues. To facilitate the interpretation of our results and put them into perspective,
we show the possible redistributive role that the tax receipts can play. Second, we
examine whether our results reflect the specific structure of the Swedish inheritance tax
institutions of the early 2000s by assessing what would have happened if a confiscatory
tax had been levied instead. Table 9 reports DME estimations under these extensions. In
Panel A, we show DMEs under the hypothetical scenario, that the actual inheritance tax
revenues are redistributed as lump sum transfers according to three alternative
redistributive schemes: giving to all heirs, giving to heirs with below-median wealth and
giving to heirs with wealth in the bottom quartile of the wealth distribution. The results
indicate that redistribution can strongly counteract the disequalizing effect of the
inheritance tax found in Table 8. When the revenues are redistributed among all heirs, the
equalizing effect of the inheritances increases (instead of decreases, as it did when we
only considered tax payments). Directing revenues to heirs in the bottom half or the
bottom quartile of the wealth distribution leads to further equalization. Under all three
redistribution schemes, the relative inequality falls more than in the baseline case. The
absolute dispersion is also reduced as a consequence of redistributing tax revenues. In
Panel B of Table 9, we simulate the redistribution effects under a fully confiscatory tax
to determine how much the results are due to the specific institutional structure of the
Swedish inheritance tax in the 2000s. Of course, the case of an imagined 100% inheritance
tax would most likely have implications for wealth accumulation and the amount of
inherited wealth. However, we prefer this scenario for two reasons. First, it represents
an upper level for the redistributive impact of inheritance taxation, and milder variants
will thus lead to outcomes within this case and the baseline cases. Second, it reflects an
interesting counterfactual to our main analysis, namely, the case of literally “no
inheritance”, whereas our baseline analysis compares the treatment of inheriting with an
“inheriting later” counterfactual. Panel B of Table 9 reports the results from this
exercise under the same three redistributive schemes as in Panel A. Redistributing the
revenues from a confiscatory tax clearly has a sizable impact on the distribution: giving
to everyone almost doubles the equalizing effect of inheritance, from the baseline of −7%
to −13%. When applying the directed redistributive schemes, the equalizing effect grows
even more, reducing the Gini coefficient by up to almost 22%. In summary, inheritance
taxation alone does not seem to equalize wealth; instead, it slightly reverses the
equalizing impact of inheritances. However, when inheritance tax revenues are also
considered and used for redistributive purposes, the total effect may be increased
equality.

<h>CONCLUDING DISCUSSION</h>
---------------------

Our findings of an equalizing impact of inherited wealth have implications for our
understanding of the intergenerational transmission of resources and for economic
inequality in general. First, if the poor tend to consume new wealth and the rich are more
likely to save it, then the theory predicts the transmission impact to be one of
disequalization, as noted by Scholz (2003). Our results are consistent with such
behavioral responses, shown by the difference between the larger DMEs and smaller BAEs.
However, these responses are not quantitatively large enough to balance the main
equalizing impact, and the equalizing impact persists at least a few years after the
inheritance treatment. Second, historical circumstances and the institutional context of
Sweden may have specific bearing on the detected patterns. Inequality in marketable wealth
in a country with an extensive welfare state is not necessarily directly comparable to
inequality in countries in which people are more reliant on their own savings. However,
since Sweden is no longer exceptional in terms of tax revenues as share of GDP (ranked
seventh in 2014), our results could be well generalized to many other countries. It should
be noted, though, that a major part of the inherited wealth analyzed was generated during
the 1960s, 1970s and 1980s, a period in the Swedish history with peaking egalitarian
welfare-state policies and relatively compressed income and wealth distributions. The
years thereafter saw both liberalized policies and widening gaps. Could it be that these
historical trends in inequality and redistribution are reflected in the equalizing impact
of inheritance documented in the study, and thus that heirs not only inherited wealth but
effectively also the previous, more equal wealth distribution? At this point, we can only
speculate, but such an interpretation would be in line with Nybom and Stuhler's (2014)
recent theoretical work on the mechanisms of intergenerational transmission, showing that
past institutions and institutional change in a parental generation can have long-lasting
effects and eventually affect the offspring generation through the transmission process.
On the other hand, our findings are in line with the previous results from Europe, Japan,
and the United States, suggesting that inheritances equalize the wealth distribution in
many countries. Moreover, the fact that the inheritance law stipulates that heirs do not
inherit any debts the decedent may have upon death also contributes to the equalizing
effects of inheritances that we find. The Swedish inheritance law is, however, not unique
in this feature. In most countries, debts are not passed on to the heirs and even in
countries where they are (e.g., Spain and Japan), the heir can refuse the inheritance.
Third, our focus on the inequality of personal wealth leaves out other relevant
distributional dimensions. One closely related outcome is lifetime resources which is the
sum of lifetime earnings and all gifts and bequests. Lifetime earnings are more evenly
distributed and much larger than the sum of gifts and bequests, and this could make the
distributional consequences of inheritances markedly different from what we observe
(although early simulation studies by Blinder (1973) and Davies (1982) do not indicate
such marked differences). From a more general perspective, investigating how inheritances
affect other aspects of inequality, such as income, leisure, consumption and health, would
be interesting.


<h>REFERENCES</h>
----------

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<ART>Keep up with the winners: Experimental evidence on risk taking, asset integration, and peer effects
================================================================================

Authors: Marcel Fafchamps, Bereket Kebede, Daniel John Zizzo
DOI: 10.1016/j.euroecorev.2015.07.001
Year: 2015  |  Pages: 59-79
ASJC codes: 2002, 2003
Keywords: Asset integration, Prospect theory, Risk, Social comparisons

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

The paper reports the result of an experimental game on asset integration and risk taking. We find some evidence that winnings in earlier rounds affect risk taking in subsequent rounds, but no evidence that real life wealth outside the experiment affects risk taking. Controlling for past winnings, participants receiving a low endowment in a round engage in more risk taking. We test a 'keeping-up-with-the-Joneses' hypothesis and find that subjects seek to keep up with winners, though not necessarily with average earnings. Overall, the evidence suggests that risk taking tracks a reference point affected by social comparisons.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

In spite of a voluminous literature in psychology and economics, risk taking decisions
remain poorly understood. This is unfortunate given how critical risk taking is to
important economic decisions. We use an original experiment to revisit a key issue that
potentially affects risk taking: asset integration. This refers to the idea that
individuals decide about risky prospects by considering the effect of decisions on their
final wealth rather than on specific gains and losses (Kahneman and Tversky, 1979). We
focus on two kinds of asset integration: (1) integration of winnings between successive
tasks within an experiment; and (2) integration of winnings with real life wealth outside
the experiment. We also examine whether risk taking is affected by social comparisons,
while controlling for other factors that may affect risk taking, such as learning and
imitation. The study population, partly made of Ethiopian farmers, faces considerable risk
in their daily life and is thus well suited to investigate risk taking. Furthermore,
because this population is poor, the winnings from the experiment are large relative to
their normal income. We thus expect their behavior to be more representative of risk
taking by experienced individuals. We also present evidence using university students in
the United Kingdom and in Ethiopia. There is evidence that experimental subjects make risk
taking decisions ‘as in a bubble׳, that is, ignoring their non-experimental assets.2
Perhaps the most convincing evidence of this is that experimental subjects reject
profitable lotteries involving payoffs that are small relative to their wealth (Rabin,
2000; Rabin and Thaler, 2001; Johansson-Stenman, 2009). If participants integrated lottery
stakes with their total wealth, only extremely risk averse individuals would avoid small
profitable lotteries. One way to solve this paradox is to assume that individuals keep
total wealth and experimental income mentally separate, which amounts to a lack of asset
integration (Cox and Sadiraj, 2006). This was already implied by the risk attitude
estimates of Binswanger (1981) and Gertner (1993), and has most recently been claimed by
Schechter (2007). While asset integration has been tested using experimental data alone
(e.g., Heinemann, 2008), we are aware of only one published study (Andersen et al., 2011)
that directly tests asset integration by combining survey and experimental data.3 They
find evidence of only partial asset integration. We revisit this issue using results from
a multiple round experiment and test whether people integrate winnings between successive
rounds of the same experiment. Participants are divided into groups of six. At the
beginning of each round, three receive a high endowment while the other three receive a
low endowment. Initial endowments are common knowledge within the group. From this
endowment, participants are asked how much they wish to ‘invest’ in a lottery that yields,
with equal probability, 0 or three times the amount invested. In the context of the
experiment, risk taking is represented by the share of the endowment that players invest
in the lottery. We take advantage of the fact that players are faced with the same
decision three times to investigate dynamic individual and peer effects. We begin by
showing that risk taking within the experiment is uncorrelated with the assets that
participants hold outside the experiment, i.e., there is failure of integration with real
life assets. For the Ethiopian subject population, we find that winnings from earlier
rounds of the experiment increase risk taking. This result does not hold for UK subjects.
Taken in combination, these results are consistent with narrow framing: what happens
during the experiment is regarded by participants as being in a different frame from their
daily lives4. But the size of the frame within the experiment may vary across populations.
We also test whether risk taking depends on receiving a low or high endowment in a round.
In an expected utility framework, the effect of a high endowment is predicted to be the
same as that of past winnings, i.e., positive with an equal coefficient. This is not what
we find: participants who receive a high endowment in a round invest a smaller share of it
in the lottery than those who receive a low endowment, controlling for past winnings. This
suggests that participants who receive a low endowment in a round try to make up for it by
taking more risk. This effect can be understood as an application of prospect theory to
our experimental setting, and suggests that reference points are affected by the endowment
that participants receive at the beginning of each round. We investigate whether reference
points are affected by the winnings of peers.5 At the end of each experimental round,
participants observe the winnings and investment decisions of other players in their
group. We examine whether risk taking is affected by how much others invested and won.
There are several possible channels by which these may influence risk taking. We test –
and reject – several of these channels. The results we emphasize here suggest that
subjects’ risk taking is affected by social comparisons. We find that experimental
subjects act as if they are in an implicit competition with each other: when others win
big, they take more risk, presumably to try to keep up with them. We also investigate
whether participants behave in a way similar to ‘keeping up with the Joneses’ in the
consumption domain (Duesenbery 1949; Johansson-Stenman et al., 2002).6. One simple way of
modelling this is by assuming that the reference point or aspiration level is a function
of what others earn on average: if participants are falling behind the average of their
peers, they then take more risk – up to the point where they are above the average.7 This
idea is reminiscent of Bault et al. (2008) although their experimental setting is
different. We test this prediction and find no evidence of such an effect. Taken together,
the results indicate that experimental subjects take experimental earnings into account
when deciding how much risk to take: some subject populations (i.e., in Ethiopia but not
in the UK) take more risk if they won more in earlier rounds; all seek to compensate for a
low endowment in a round by taking more risk; and all take more risk if some players in
their group won more than them in earlier rounds. The latter behavior suggests that
participants take high earners as reference point when deciding how much risk to take.
Risk taking thus appears to have a competitive element, even when participants are quite
poor and when the potential earnings from the experiment are large relative to their
wealth or income.

<h>THE EXPERIMENT</h>
--------------

We conducted an experiment in Ethiopia in four rural villages, mainly with farmers, and
with university students in the capital city, Addis Ababa. As robustness check, the
experiment was subsequently replicated in the UK. The details and findings of the UK
replication are discussed in the robustness section. The rural fieldwork in Ethiopia was
conducted between February and March 2009. The four villages are located in different
agro-ecological regions of the country. Subjects were recruited among household heads and
their spouses participating in the Ethiopian Rural Household Survey panel. All
participants come from farming households; two-third of them are males. The games with
university students took place in February 2010. Addis Ababa university did not have a
permanent experimental laboratory at the time so students were recruited through ads
posted around campus. Information about participants is given in the Data Section. The
experimental design is based on earlier experiments organized by Zizzo (2003) and Zizzo
and Oswald (2001) in a laboratory setting. Participants are asked to repeatedly make the
same risky choice. This choice is framed as an investment decision. This enables us to
examine whether choices evolve over time as a function of each participant׳s past winnings
and information set. This aspect of the data is the focus of this paper.8 The design of
the experiment is as follows. Thirty individuals participate in a session and these
players are divided into five groups with six players in each, equally divided into high
and low income players. Anonymity within each group is strictly maintained even though the
thirty participants in a session can see each other. Each player plays three rounds. At
the start of each round players are randomly given either a high (Ethiopian Birr 15) or a
low (Birr 7) endowment to induce inequality.9 Each participant then decides how much of
this endowment to invest in a more than actuarially fair lottery with a 50% chance of
winning thrice the amount invested. Lottery outcomes are independent across participants.
After lottery winnings are determined, players are informed of the winnings of the other
five members of their group and how much they themselves have won from the lottery. The
game is repeated three times.10 In each round new groups are formed with different
participants. Players are informed about this. At the end of the game, participants leave
with all the winnings accumulated over the three rounds plus a participation fee. This was
implemented in four rural villages with a total number of 240 participants, and with 60
university students in the city of Addis Ababa. In addition, a slightly different version
of the game was played with another 60 students. In this version, participants stay in the
same group of six players over the three rounds. We call this treatment the fixed group
treatment.11

<h>TESTING STRATEGY</h>
----------------

We now introduce the econometric testing strategy. After presenting our notation, we
explain how we test whether participants integrate their assets or past winnings when
deciding how much risk to take. We then introduce social comparisons. At the end of the
section we discuss how we address possible confounding effects induced by imitation and
learning. Possible confounding effects are discussed in detail in Appendix.

<hs>  Risk taking</hs>
  ~~~~~~~~~~~

A positive a implies increasing relative risk aversion over the narrow range of values
taken by Zit, something that is a priori unlikely among poor subjects. It is also
difficult to reconcile b=0 with expected utility. We revisit these issues below when we
introduce reference points and loss aversion.15

<hs>  Social comparisons and relative utility</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

According to prospect theory, risk taking behavior depends on whether the decision maker
is below or above his/her reference point (Kahneman and Tversky, 1979). Above the
reference point, individuals are predicted to behave in the standard risk averse fashion.
Below the reference point, individuals may behave in a risk neutral or risk loving manner.
There is also a kink at the reference point, generating strong risk aversion when choosing
between prospects just above and below the reference point. The largely unanswered
question is what the reference point is (Koszegi and Rabin, 2006, 2007). If the reference
point responds to what happens to peers, this opens the door to the possibility that risk
taking is affected by social comparisons (e.g., Gill and Prowse, 2012).

     <hss>Keeping up with the winners</hss>

        This idea is related to the experimental evidence provided by Bault et al. (2008).
        But our experimental setting is different. Unlike Bault et al. (2008) and Linde
        and Sonnemans (2012), in our experiment social comparisons between subjects are
        not made salient by design. Furthermore, our subjects are not asked to choose
        between positively and negatively correlated outcomes. Rather they receive
        endowments that are, by design, negative and positively correlated with others in
        their group. Having received a different endowment, they are then given an
        opportunity to risk part of it, a dimension that is not present in these other
        papers.

<h>THE DATA</h>
--------

In Table 1 we present descriptive statistics on participants from the four rural sites and
for university students. Most participants are males but the proportion of males rises to
90% in the case of university students. Unsurprisingly, the average age of rural
participants is higher than that of students. On average university participants take more
risk: they invest a little over half of their initial endowment in the lottery, which is
nearly twice as much as rural players; and the cumulative distribution of investment rates
among students is everywhere above that of rural participants. University participants
invest their entire endowment in 22% of the games compared to 3% of rural participants.
Less than 1% of students invest nothing on lottery compared to 8% of rural participants.
Hence, we clearly see higher risk taking among students compared to rural participants. If
we assume, as is reasonable in the Ethiopian context, that university students have a
higher permanent income, this is consistent with the idea that income affects risk taking.
Other factors could also account for this difference – e.g., more risk taking by
university students could be explained by higher cognitive abilities (e.g., Dohmen et al.,
2010). Since taking risk is profitable in our experiment, it is not surprising to find
that the lottery winnings of the students are on average higher than that of rural
participants. Rural participants are covered by earlier household surveys from which we
recover the value of their household assets. Household assets include agricultural tools
like hoes and ploughs, household furniture and items like beds, tables, chairs and stoves
and other valuables like jewelry and watches. Rural households hardly use financial
assets. The value of household assets is a very good proxy for household income/wealth
(e.g., Filmer and Pritchett, 2001). There is a lot of variation in wealth and expenditure
within the participating rural population, as is clear from Table 1. Since there is no
corresponding survey of university students, there is no information on their household
assets. But even if we did have this information, it is unclear how informative it would
be: education is probably a better predictor of students’ expected life earnings than
whatever assets they may have. For farmers, average winnings from the experiment are
equivalent to 1.5% of household assets. Average winnings for students are even larger in
absolute terms. This ensures that the experiment provides sufficiently high powered
incentives. There is no variation in the educational level of university participants as
all of them are in higher education. Rural participants are more representative of the
Ethiopian adult population, with much lower education levels. Half of rural participants
have no formal education and more than 80% have at most incomplete primary education.23
Although vocational skills may increase agricultural productivity, only 2% of rural
participants have any form of vocational training. The heterogeneity of the country in
terms of religious beliefs is reflected in the subject population. In both sites, the
traditional Ethiopian Orthodox faith is the most common, followed by Protestantism.
Muslims are underrepresented compared to the Ethiopian population at large.

<hs>  Asset integration</hs>
  ~~~~~~~~~~~~~~~~~

We report three versions of each regression with different controls. The first version
(columns 1, 4 and 7) only includes the above-mentioned regressors plus dummy variables for
each of the experimental sites to control for differences in average attributes across
sites. The second version (columns 2, 5 and 8) adds controls for whether the composition
of the groups was the same across rounds or not, and for whether the experimental session
took place in the afternoon – to control for possible mood effects correlated with time of
day (e.g., Coates and Herbert, 2008). As further robustness check, the third version
(columns 3, 6 and 9) adds individual controls such as age, gender, education and religion
which may be correlated with risk taking. To investigate whether our results are an
artifact of censoring, we reestimate Table 2 with a tobit estimator that allows for a
lower limit of 0 and a variable upper limit Zit. Results, not reported here to save space,
are very similar to those in Table 2 in terms of coefficient magnitude and significance.
This is hardly surprising given that few observations are at the upper limit of Xit: 4.2%
of high endowment observations take value 15 and 14.8% of low endowment observations take
value 7.

<hs>  Social comparisons</hs>
  ~~~~~~~~~~~~~~~~~~

We also estimate model (KW) which is linear in Rit. If i׳s reference point is well above
the average as in KW, we should only observe the declining portion of Fig. 2. As shown in
Table 7, Rit has a significantly negative sign in 5 of the 6 regressions in linear form,
as predicted by KW. Taken together, Tables 6 and 7 thus suggest that subjects want to keep
up with above average players, that is, with the winners.27

<hs>  Robustness checks</hs>
  ~~~~~~~~~~~~~~~~~

In addition, we investigate whether our results are an artefact of pooling student and
rural subjects. To test the validity of pooling, we reestimate all Tables (except 3 and 4,
which only apply to rural subjects) with interaction terms between regressors and a
student dummy. Results are shown in online appendix Tables A2b–A10b. In the overwhelming
majority of cases the interactive terms are not significant: of all the 135 interactive
terms in all the regressions, only 12 are significant at the conventional level of 5%. Our
conclusions stand even when we control for possible heterogeneity between students and
rural subjects.

<hs>  Replication of the experiment</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As a final robustness check, we replicate the experiment with a different subject
population, namely with College students at the University of East Anglia (UEA), United
Kingdom. We ran 8 sessions of 12 participants each. Subjects are drawn from the pool of
student subjects registered with the UEA experimental laboratory. To maximize
comparability, the experimental protocol is as close as possible to that used in Ethiopia,
and is virtually identical to that of Addis Ababa students. In particular, we use the same
pen-and-paper design. The details of the experimental design are the same as those for the
Ethiopia sessions. We took advantage of the replication experiment to take up on a
suggestion made by one of the referees and echoed by the editor. In the original
experiments, half of the subjects in a group receive an endowment of 7 and the other half
received 15. Results show that subjects who receive 7 invest proportionally more than
those who receive 15. This finding is hard to explain from expected utility, but can
easily be accounted for using prospect theory if subjects have a reference point situated
above 7. What is unclear is whether this high reference point comes from observing other
subjects receiving 15 – which could constitute additional evidence of a ‘keeping up with
the winners’ effect. To test whether the high reference point comes from observing other
subjects ‘winning’ a larger endowment, we introduce two new treatments that only differ in
terms of the endowment received at the beginning of each round. In the original experiment
3 subjects receive 7 and 3 others receive 15 (normal treatment). In the two new
treatments, all 6 subjects in a group receive the same endowment, i.e., either be 7 (low
treatment) or 15 (high treatment). By comparing subjects who receive 7 in a low treatment
to those who receive 7 in the normal treatment, we can test whether their investment
decisions are the same. If it is, this suggests that the high reference point does not
come from observing other subjects receiving 15. For the rest, the experiment is the same
as in Ethiopia with one caveat: in 6 of the 8 sessions we omit money burning. The purpose
of this omission is to check the robustness of our findings to the absence of money
burning. To summarize, treatments are as follows: T1, T2 and T3 are the normal, high, and
low treatments, respectively – all without money burning. Treatment T4 is the normal
treatment with money burning. We observe a number of behavioral similarities in the UEA
and Ethiopia subject pools. Risk taking xit is higher for subjects who receive 7 than for
those who receive 15 across all treatments, and this difference is strongly significant
when we compare low and high endowment subjects within treatments T1 and T4: 56% versus
32% with p-value=0.0000 in T1; and 63% versus 46% with p-value of 0.0007 in T4. When we
compare low endowment subjects in the normal (T1) and low (T3) treatments, we find
virtually identical risk taking xit: 56% versus 58% with a p-value of 0.64. Similarly,
when we compare low endowment subjects in treatments T3 and T4, we find that differences
in average risk taking go in the anticipated direction but are not statistically
significant: 58% versus 63% with a p-value of 0.22. From this we conclude that the
endowment received by other players in the group is not what drives high reference points.

<h>DISCUSSION AND CONCLUSION</h>
-------------------------

Using data on repeated risk taking in a sequential experiment, we have tested whether
participants׳ behavior follows some commonly hypothesized patterns of behavior. Our key
findings can be summarized as follows: Asset integration with total wealth: We find no
evidence of asset integration between the experimental tasks and real world wealth.
Participants apply a narrow framing by which they segregate the set of tasks at hand from
their outside wealth . This finding provides support to the intuition of much of the
literature and, if anything, is particularly strong evidence of narrow framing given that
stakes are large relative to participants׳ normal income and that, unlike Andersen et al.
(2011) who find at least some effect, we find no evidence that risk taking responds to
wealth. Asset integration across experimental rounds: for the Ethiopia sample there is
evidence that winnings from earlier rounds raise risk taking in later rounds; for the UK
sample the evidence goes in the opposite direction. High reference point: Within each
round, participants who receive a small endowment risk a higher share of it. This finding
is difficult to account for under a reasonable expected utility model. But it can be
explained if the aspiration level of low endowment recipients is higher than their
endowment. For example, under loss aversion and a high enough reference point (due to this
social comparison or otherwise), participants who receive a low endowment may seek to make
up for it by risking relatively more than if they had received a high endowment. This
finding holds in both the Ethiopia and UK samples. ‘Keep up with the winners’: We observe
that subjects risk more when other participants they can observe have higher past
winnings. We interpret this finding as suggesting that the reference point that subjects
use increases in the winnings of others. Hence when others win more, they risk more in an
attempt to catch up. This finding holds in both the Ethiopia and UK samples. In Appendix
we test and reject the possibility that this may be due to imitation or to gambler׳s
fallacy. ‘Keep up with the average’: We only find limited support for it in our
experiment. Participants do take more risk when their past winnings are below that of the
average of their peers, but not in a way that suggests they regard the average winnings of
others as reference point. Combined with earlier results, this confirms that participants
seek to keep up with winners, but not with the average. We believe that two of the above
results are of particular interest. First, the evidence suggests that participants seek to
keep up with the winners. This finding complements existing experimental evidence on
social comparisons (e.g., Bault et al., 2008, Linde and Sonnemans, 2012). It highlights
the need for further research to ascertain how sensitive social comparisons are to framing
and to information about others׳ earnings. Second, for the Ethiopia sample – but not the
UK sample – we cannot reject full integration of winnings within the experiment. We also
find no evidence of asset integration beyond the narrow frame of the experiment. The
Ethiopia findings provide some support for Cox and Sadiraj (2006) and Cox et al. (2008)
distinction between total wealth and income and confirm the need to separate the two when
estimating risk attitude in applied research. They also raise the question of how to
interpret models that link risk attitude with overall wealth and income inequality in a
population (e.g., Becker et al., 2005; Hopkins and Kornienko, 2010; Hopkins, 2011). One
possible interpretation of these models is that economic agents are in a wealth tournament
with everyone else in the population. The evidence presented here suggests that this
interpretation may be unwarranted, in the sense that agents may not see themselves as part
of a tournament involving their overall integrated wealth, but rather of one involving
incomes earned in specific micro-decision environments (such as our experiment). More
research is needed to ascertain whether our findings generalize outside our experimental
setup.


<h>REFERENCES</h>
----------

  [2] Rachel Croson, Uri Gneezy. Gender differences in preferences. doi:10.1257/jel.47.2.448
  [3] Jona Linde, Joep Sonnemans. Social comparison and risky choices. doi:10.1007/s11166-011-9135-z
  [4] J. M. Coates, J. Herbert. Endogenous steroids and financial risk taking on a London trading floor. doi:10.1073/pnas.0704025105
  [5] James C. Cox, Vjollca Sadiraj. Small- and large-stakes risk aversion: Implications of concavity calibration for decision theory. doi:10.1016/j.geb.2005.08.001
  [6] James C. Cox, Vjollca Sadiraj. Risky decisions in the large and in the small: Theory and experiment. doi:10.1016/S0193-2306(08)00002-1
  [8] Thomas Dohmen, Armin Falk, David Huffman, Uwe Sunde. Are risk aversion and impatience related to cognitive ability?. doi:10.1257/aer.100.3.1238
  [9] Deon Filmer, Lant H. Pritchett. Estimating wealth effects without expenditure data - Or tears: An application to educational enrollments in states of India. doi:10.2307/3088292
  [10] Robert Gertner. Game shows and economic behavior: Risk-taking on “card sharks”. doi:10.2307/2118342
  [11] David Gill, Victoria Prowse. A structural analysis of disappointment aversion in a real effort competition. doi:10.1257/aer.102.1.469
  [12] Frank Heinemann. Measuring risk aversion and the wealth effect. doi:10.1016/S0193-2306(08)00005-7
  [14] Ed Hopkins, Tatiana Kornienko. Which Inequality? The inequality of endowments versus the inequality of rewards. doi:10.1257/mic.2.3.106
  [15] Olof Johansson-Stenman. Risk aversion and expected utility of consumption over time. doi:10.1016/j.geb.2009.07.001
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  [19] Botond Köszegi, Matthew Rabin. A model of reference-dependent preferences. doi:10.1162/qjec.121.4.1133
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  [22] Matthew Rabin, Richard H. Thaler. Anomalies: Risk aversion. doi:10.1257/jep.15.1.219
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  [24] Laura Schechter. Risk aversion and expected-utility theory: A calibration exercise. doi:10.1007/s11166-007-9017-6
  [25] Daniel John Zizzo. Money burning and rank egalitarianism with random dictators. doi:10.1016/S0165-1765(03)00190-3
  [27] Nadège Bault, Giorgio Coricelli, Aldo Rustichini. Interdependent utilities: How social ranking affects choice behavior. doi:10.1371/journal.pone.0003477
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<ART>Labor income dynamics and the insurance from taxes, transfers, and the family
=============================================================================

Authors: Richard Blundell, Michael Graber, Magne Mogstad
DOI: 10.1016/j.jpubeco.2014.04.011
Year: 2015  |  Pages: 58-73
ASJC codes: 2002, 2003
Keywords: Income dynamics, Insurance, Life cycle inequality

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

What do labor income dynamics look like over the life-cycle? What is the relative importance of persistent shocks, transitory shocks and heterogeneous profiles? To what extent do taxes, transfers and the family attenuate these various factors in the evolution of life-cycle inequality? In this paper, we use rich Norwegian population panel data to answer these important questions. We let individuals with different education levels have a separate income process; and within each skill group, we allow for non-stationarity in age and time, heterogeneous experience profiles, and shocks of varying persistence. We find that the income processes differ systematically by age, skill level and their interaction. To accurately describe labor income dynamics over the life-cycle, it is necessary to allow for heterogeneity by education levels and account for non-stationarity in age and time. Our findings suggest that the redistributive nature of the Norwegian tax-transfer system plays a key role in attenuating the magnitude and persistence of income shocks, especially among the low skilled. By comparison, spouse's income matters less for the dynamics of inequality over the life-cycle.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The aim of this paper is to examine the dynamics of labor income over the working life and
to explore the impact of two mechanisms of attenuation or insurance to labor income
shocks. The first is the tax and transfer system; the second is spouse's income. We focus
on three dimensions of inequality: individual market income, individual disposable income,
and family disposable income; and explore the relationship between them over the life-
cycle. Our objective is to provide a detailed picture of the dynamics of inequality over
the life-cycle, following individuals from many different birth cohorts across their
working lifespan. By linking up individuals with other family members, we are able to
examine the impact of spouse's income and the role of the tax–transfer system as
mechanisms to smooth shocks to individual market income. There are a number of key
questions addressed. What do labor income dynamics look like over the life-cycle? What is
the relative importance of persistent shocks, transitory shocks and heterogeneous
profiles? To what extent does the tax and transfer system attenuate these various factors
in the evolution of life-cycle inequality? What happens when we add in income sources of
spouses? Answering these questions has proved to be quite difficult. One problem that is
often argued to hinder analysis is data availability. While the ideal data set is a long
panel of individuals, this is somewhat a rare event and can be plagued by problems such as
attrition and small sample sizes. An important exception is the case where countries have
available administrative data sources. The advantages of such data sets are the accuracy
of the income information provided, the large sample size, and the lack of attrition,
other than what is due to migration and death. To investigate the above questions, we
exploit a unique source of population panel data containing records for every Norwegian
from 1967 to 2006. Norway provides an ideal context for this study. It satisfies the
requirement for a large and detailed data set that follows individuals and their family
members over long periods of their working career. It also has a well developed
tax–transfer system, and our data provides us with a measure of income pre and post the
payment of taxes and the receipt of transfers. To understand the role of taxes, transfers
and the family in attenuating shocks to labor income requires a model that allows for key
aspects in the evolution of labor income over the life-cycle. The extensive literature on
the panel data modeling of labor income dynamics points to three ingredients of potential
significance: shocks of varying persistence; age and time dependence in the variance of
shocks; and heterogeneous age profiles. For example, our long panel data allows us to
decompose income shocks at every age into two components: one is mean-reverting over short
periods (we label ‘transitory’ shocks), while the other could either be permanent or
persistent and mean-reverting over long periods (we label ‘permanent’ shocks). By way of
comparison, the usual random walk specification would restrict the permanent shocks to be
truly permanent rather than merely persistent. Additionally, by following many different
birth cohorts across their working lifespan we are able to allow a flexible structure for
time effects in deriving our life-cycle profiles.1 The size and detailed nature of the
data we are using allow us to explore the importance of these three ingredients for labor
income dynamics. Our key findings on the labor income dynamics of males are three-fold.
First, the magnitude of permanent and transitory shocks varies systematically over the
life-cycle. Indeed, we may strongly reject the hypothesis of age-independent variance of
shocks. Second, there is essential heterogeneity in the variances of permanent shocks
across skill groups. For low skilled, the magnitude of permanent shocks is monotically
increasing in age. For example, a permanent shock of one standard deviation implies a 35%
change in individual market income for a low skilled 30 year old; the corresponding number
for a low skilled 55 year old is 50%. High skilled, on the other hand, experience large
permanent shocks early in life; these shocks decrease in magnitude until age 35, after
which they are relatively small and fairly stable. Third, the variance of transitory
shocks exhibits a decreasing profile over the life-cycle. While this findings holds for
all skill groups, high skilled tend to experience relatively large transitory shocks early
in life. The evidence of heterogeneity in the dynamics of labor income by age, skill
level, and their interaction motivates and guides our analysis of the insurance from
taxes, transfers and the family. We find that the tax–transfer system reduces both the
level and persistence of shocks to labor income. In particular, taxes and transfers lead
to a remarkable flattening of the age profiles in the variances of permanent and
transitory shocks for the low skilled. At age 55, for example, a permanent shock of one
standard deviation implies a 50% change in annual market income for a low skilled; the
corresponding number for annual disposable income is only 31%. After taking taxes and
transfers into account, spouse's income matters little for the dynamics of inequality over
the life-cycle. Taken together, our results suggest that a progressive tax–transfer system
could be an important insurance mechanism to labor income shocks, especially for low
skilled. These results may have implications for both policy and a large and growing
literature on consumption inequality and the overall ability of families to insure labor
income shocks (see e.g. Blundell et al., 2012). Economic theory predicts that consumption
responds strongly to highly persistent or permanent shocks, and empirical evidence
suggests little if any self-insurance in response to permanent shocks among individuals
with no college education (see e.g. Blundell et al., 2008). Our study points to the
importance of understanding the nature of risk that families face over the life-cycle, and
the extent to which taxes and transfers crowd out or add to the insurance available in
financial markets, the family or other informal mechanisms. Our paper also contributes to
the literature on modeling of labor income dynamics. Identification of credible income
processes is key for answering a number of important economic questions, including life-
cycle consumption and portfolio behavior (see e.g. Gourinchas and Parker, 2002), the
sources of inequality (see e.g. Huggett et al., 2011), and the welfare costs of business
cycles (see e.g. Storesletten et al., 2001, 2004). The conclusions reached about these
questions likely depend on the specification of the labor income process used to calibrate
the models. The relatively small scale of the available U.S. panel surveys has forced
researchers to rely on simple models that impose economically implausible restrictions
(see the discussions in Baker and Solon, 2003; Meghir and Pistaferri, 2011). Using rich
Canadian data from 1976 to 1992, Baker and Solon (2003) reject several of these
restrictions, including no life-cycle variation in the variance of transitory shocks.2
DeBacker et al. (2013) use a large panel of tax returns to study income dynamics in the
U.S. over the period 1987–2009.3 Their estimates point to the importance of allowing for
time dependence in the variance components of income. Our study complements these studies
by bringing new evidence on several issues pertinent to modeling of income processes. One
key finding is that allowing for both age and time dependence in the variance components
is essential to accurately describe labor income dynamics. In particular, when restricting
the variances of the error components to be constant across the life-cycle, we miss the
large permanent shocks that occur late (early) in life for the low (high) skilled. Another
key finding is that allowing for heterogeneity by education levels is necessary to capture
labor income dynamics of young and old workers. When we restrict the income processes at
the variance level to be the same across skill groups, we find a U-shaped age profile in
the variances of permanent shocks; however, this pattern is at odds with the age profiles
of both high and low skilled.4 By way of comparison, the dynamics of income over the life-
cycle change little when restricting the transitory shocks to be uncorrelated over time or
allowing for heterogeneous experience profiles within each skill group. Indeed, only for
the high skilled, there is evidence of significant unobserved heterogeneity in the income
growth rates. Accounting for this heterogeneity lowers the overall persistence of income
shocks somewhat, but barely moves the age profiles in the variances of permanent and
transitory shocks. The remainder of the paper proceeds as follows. Section 2 presents our
data and discusses institutional details. Section 3 describes our panel data specification
for income dynamics and presents our findings on the labor income process of males.
Section 4 explores the degree of insurance provided by taxes and transfers as well as the
income of the spouse. Section 5 offers evidence on several issues pertinent to modeling of
income processes. Section 6 concludes.

<hs>  Data and sample restrictions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our analysis employs several registry databases maintained by Statistics Norway that we
can link through unique identifiers for each individual. This allows us to construct a
rich longitudinal data set containing records for every Norwegian from 1967 to 2006. The
variables captured in this data set include individual demographic information (including
gender, date of birth, and marital status) and socioeconomic information (including years
of education, market income, cash transfers). The data contains unique family identifiers
that allow us to match spouses and parents to their children. The coverage and reliability
of Norwegian registry data are considered to be exceptional (Atkinson et al., 1995).
Educational attainment is reported by the educational establishment directly to Statistics
Norway, thereby minimizing any measurement error due to misreporting. More importantly,
the Norwegian income data have several advantages over those available in many other
countries. First, there is no attrition from the original sample because of the need to
ask for permission from individuals to access their tax records. In Norway, these records
are in the public domain. Second, our income data pertain to all individuals and all jobs,
and not only to jobs covered by social security. Third, we have nearly career-long income
histories for certain cohorts, and do not need to extrapolate the income profiles to ages
not observed in the data. And fourth, there are no reporting or recollection errors; the
data come from individual tax records with detailed information about the different
sources of income. We study income dynamics for the 1925–1964 annual birth cohorts during
the period 1967–2006. The reason for this selection of cohorts is to ensure fairly long
records on earnings for each individual. We restrict the sample to males, to minimize
selection issues due to lower labor market participation rates for women in the early
periods. In line with much of the previous literature, we exclude immigrants and self-
employed. We further refine the sample to be appropriate for our analysis of labor income
dynamics. In each year, we select males who are between the ages of 25 and 60. These
individuals will likely have already completed most of their schooling and are too young
to be eligible for early retirement schemes. In our baseline specification, we further
restrict the sample to individuals with at least four subsequent observations with
positive market income. This restriction gives us the largest possible sample, given that
transitory shocks are assumed to follow a first-order moving average process. Applying
these restrictions provides us with a panel data set with 40 time periods and 934,704
individuals. We will refer to this as the baseline sample. On average, this sample
consists of 23,368 individuals per birth cohort. Our model estimates age-specific variance
components from age 26 to 58. By following many birth cohorts, we are able to allow a
flexible structure for calendar time effects in deriving our life-cycle profiles. For the
1942–1946 cohorts, we observe income at every age. For the cohorts born earlier
(1925–1941), we miss one or more income observations between the ages of 25 and 41. For
the cohorts born later (1947–1964), income is no longer observed at some point after age
42. As a result, our age-specific estimates are based on an unbalanced panel of income.
Appendix Fig. C.1 shows the sample size by age. The number of observations declines late
(early) in the working lifespan because we are not observing the labor income of younger
(older) cohorts at these ages. It is therefore reassuring that the mean and variance of
income display similar shapes over the life cycle across cohorts. The income variables
that we consider are defined as follows. The first variable is individual market income,
defined as the annual pretax earnings.5 The second variable is individual disposable
income, incorporating annual earnings and cash transfers net of taxes.6 The third variable
is family disposable income. Our measure of family disposable income pools the individual
disposable income of the spouses (if the male has a spouse). Throughout the analysis, we
partition the baseline sample into three mutually exclusive groups according to
educational levels. The reason is that previous studies point to heterogeneity in the
dynamics of labor income by educational levels. Low skilled is defined as not having
completed high school (32% of the baseline sample), medium skilled includes individual
with a high school degree (48% of the baseline sample), and the high skilled consists of
individuals who have attended college (20% of the baseline sample).

<hs>  Institutional details and descriptive statistics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Before turning to the estimation of the income processes, we describe a few important
features of our data and the Norwegian setting. We first consider the pattern of labor
market participation over the life cycle. Appendix Fig. C.2 shows the population share of
males with positive market income by age. We see that the labor market participation rate
starts out at around 90% when individuals are young. The participation rate remains at
this high level until individuals reach their 50s, at which point they start exiting the
labor market at an increasing rate. In particular, low skilled individuals are relatively
likely to exit the labor market before they can receive (early) retirement benefits.
Appendix Fig. C.3 shows the levels and growth rates in market income by the age at which
individuals exit the labor market. We see that early exits from the labor market are
associated with low and declining market income in the years prior to exit. Given the
sample restriction of non-zero market income, our baseline sample will therefore be of
higher quality toward the end of the life-cycle (especially among the low educated). This
should put downward pressure on the magnitude of shocks late in life, and most likely give
us a lower bound on the insurance from taxes and transfers at these ages. Next, we
consider how individual market income varies over the life-cycle in our baseline sample.
Fig. 1 shows the age profiles in the different measures of income by education levels.
Each market income profile displays the familiar concave shape documented and analyzed by
Mincer (1974), but the college-educated workers experience more rapid market income growth
early in the working lifespan. Fig. 2 shows the variance of log market income over the
life-cycle according to education levels. In line with the prediction of the Mincer model,
the variances of medium and high skilled have a U-shaped profile.7 Among low skilled, the
variance of log market income is weakly increasing until they are in their mid 40s, after
which it rises rapidly. We then examine the extent to which the tax and transfer system
affects the mean and the variance of log individual income over the life-cycle. Fig. 1
show how the progressive nature of the tax system dampens the income differentials between
high skilled and low skilled after age 35.8 At the same time, low skilled are more likely
to receive cash transfers while working (such as partial disability benefits), especially
toward the end of the working lifespan. Fig. 2 shows how the tax–transfer system
eliminates the increase over the life-cycle in the variance of log market income among the
low educated. By comparison, taxes and transfers do less to the large income variance
among the high skilled early in their careers. Lastly, we consider how family disposable
income varies over the life-cycle in our baseline sample. Fig. 1 compares the age profiles
in log family disposable income and log individual disposable income. In the beginning of
the working lifespan, relatively few males are married and individual disposable income is
therefore quite similar to family disposable income.9 When the males are in their mid 30s,
the vast majorities are married and the income of the spouse plays a more important role.
At this point, about 80% of the spouses are participating in the labor market, thus
contributing significantly to family income.10 Fig. 2 shows the life-cycle variation in
the variance of log family disposable income. The family income measure displays quite
similar variance over the working lifespan as compared to the measure of individual
disposable income.

<hs>  A panel data specification for labor income dynamics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

To understand the role of the tax and transfer system in attenuating shocks to income for
individuals and families over the life-cycle requires a model that allows for key aspects
in the evolution of labor market income over the working life. As we noted in the
introduction, the extensive literature on the panel data modeling of income dynamics has
pointed to three key ingredients of potential significance: shocks of varying persistence;
age and time dependence in the variance of shocks; and heterogeneous age profiles. The
size and detailed nature of the Norwegian population panel allow us to combine all three
of these components and let the degree of persistence and the variance of the shocks vary
in a quite unrestricted way by age and calendar time. In Appendix A: Estimation Details,
we describe every step of the estimation procedure for the income process given in (1).
There are, however, three important features to notice. First, we allow for the permanent
component vi,ac to have a ρc coefficient less than unity. Since we have long enough panels
for individuals in each of the cohorts, the parameters of this process together with those
for the transitory process and the heterogeneous profiles can be separately identified.
This illustrates that by allowing the variances of each component to differ by age, we are
in effect, allowing the autocorrelation of income shocks to vary quite unrestrictedly over
the life cycle (even though ρ does not depend on age). Lastly, the use of data that
follows actual cohorts over the life cycle allows us to accurately measure their true
earnings pattern and estimate the labor income dynamics experienced by individuals. The
model given in Eq. (1) is estimated separately by education levels using an equally-
weighted minimum distance approach applied to second order moments. At every age, we
average the moments across cohorts before estimating the income process.12 Without further
restrictions, the estimates can be interpreted as an average (or a typical) labor income
dynamics experienced by these cohorts over their working lifespan. Our focus is on life-
cycle effects and to determine the relative contribution of age and calendar time effects
to the labor income dynamics we require further restrictions. If one were to assume no
cohort effects, we would effectively control for calendar time effects by averaging the
moments across cohorts. Heathcote et al. (2005) argue that time effects are required to
account for the observed trends in inequality. One might, however, suspect that cohort
effects should play some role in the distribution of fixed effects. For example, rising
college enrollment rates may have changed the level of permanent wage dispersion of
younger relative to older cohorts. We incorporate this source of heterogeneity across
cohorts by estimating the income processes separately by education levels.

<hs>  Baseline estimates</hs>
  ~~~~~~~~~~~~~~~~~~

We begin by considering the labor income dynamics of males. The model given in Eq. (1) is
estimated separately by education levels.13 For now, we impose homogenous experience
profiles (βi = 0) in the estimation.14 Instead of presenting the labor income dynamics of
each cohort, we average the moments across the cohorts before estimating the income
process. As a result, the estimates should be interpreted as an average (or a typical)
labor income dynamics experienced by these cohorts over their working lifespan. The first
column of Table 1 reports the parameter estimates for individual market income of males.
For each skill group, we find that the persistence parameter (ρ) is either one or close to
one. This suggests that the shocks to (log) labor income can be described as the sum of a
transitory shock and a highly persistent process. Because of the unit root, we do not
identify the variance of initial conditions (var(αi)) for the low or medium skilled. The
more persistent the shocks, the more important it is to know whether workers at different
ages face the same variance of permanent shocks, or if the magnitude changes
systematically over the life-cycle. Fig. 3 examines this by showing the age profile in the
variance of permanent shocks (var(ui,a)) according to education levels. The magnitude of
permanent shocks varies systematically over the life-cycle. Indeed, we may strongly reject
the standard specification with age-independent variance components. Another key finding
is the heterogeneity in the variances of permanent shocks by education levels. For low
skilled, the magnitude of permanent shocks is monotically increasing in age. For example,
a permanent shock of one standard deviation implies a 35% change in individual market
income for a low skilled 30 year old; the corresponding number for a low skilled 55 year
old is 50%. High skilled, on the other hand, experience large permanent shocks early in
life; these shocks decrease in magnitude until age 35, after which they are relatively
small and fairly stable. For example, a permanent shock of one standard deviation implies
a 28% change in individual market income for a high skilled 55 years old; the
corresponding number for a high skilled 28 (40) years old is 44 (22) percent. The variance
of transitory shocks, shown in Fig. 4, exhibits a decreasing profile over the life-cycle.
While this findings holds for all skill groups, high skilled tend to experience relatively
large transitory shocks early in life. At the same time, the MA parameter differs by skill
group. A larger proportion of the transient shocks persist for another period for high
skilled workers than for low skilled workers. To see the importance of low incomes in
determining the age profiles of labor market shocks, we present results in Appendix Figs.
C.6 and C.7 where we exclude observations with low market incomes.15 The profiles are much
flatter. The presence of low market incomes early and late in life is mirrored in hours of
work over the life-cycle. When looking at decennial Norwegian Census data over the period
of study, we find that mean hours across the life-cycle is inverse U-shaped. There is an
increase until individuals are in their early 30s, then a flattening, and eventually a
decrease toward retirement. The opposite is true for the variance of log hours, which is
U-shaped. In particular, there is a sharp downward trend in the dispersion of hours worked
before age 35.16

<hs>  Model fit</hs>
  ~~~~~~~~~

We now examine the performance of the model given in Eq. (1) in fitting the variance of
(residual) income growth rates as well as one-lag covariances. For each income measure and
every skill group, we conclude that the baseline specification with homogenous profiles
(βi = 0) and a MA(1) achieves a very good fit of these key moments over the life-cycle.
Appendix Fig. C.10 shows the model fit for the variance of the growth rate, while Appendix
Fig. C.11 displays the match for the one-lag covariance profile of the growth rate. We
find that the model matches the variance of the growth rate observed in the data almost
perfectly. When ρ = 1, we effectively target the variance of the growth rate in the
estimation. As a result, the age dependence of the variances shocks allows us to match the
age profile very well. When ρ < 1, the moments used in the estimation differ from those
shown in the figure. It is therefore reassuring to find that the model also in this case
fits the data very well.

<h>INSURANCE FROM TAXES, TRANSFERS AND THE FAMILY</h>
----------------------------------------------

The evidence of heterogeneity in the dynamics of labor income by age, skill level, and
their interaction raises a number of important questions. To what extent does the tax and
transfer system attenuate or insure the shocks to market income at different parts of the
life-cycle? Does the addition of income sources from the spouse offset or enhance labor
market shocks? In this section, we investigate these questions.

<hs>  Taxes and transfers</hs>
  ~~~~~~~~~~~~~~~~~~~

The second column of Table 1 reports the estimation results for individual disposable
income of males. Importantly, the tax–transfer system reduces the level and persistence of
both the permanent and the transitory shocks. The estimated persistence parameter falls
the most for low skilled; when ρ = 0.87, the effect of an income shock is reduced to 25%
of its initial value in ten years. At the same time, Figs. 3 and 4 show that taxes and
transfers lead to a remarkable flattening of the age profiles in the variances of
permanent and transitory shocks for the low skilled. At age 55, for example, a permanent
shock of one standard deviation implies a 50% change in annual market income for a low
skilled; the corresponding number for annual disposable income is only 31%. Shifting
attention to the high skilled, we can see that taxes and transfers do little to the age
profile in the variance of transitory shocks. As shown in Fig. 4, it exhibits a decreasing
and convex profile also in individual disposable income; indeed, the magnitudes of the
transitory shocks are only slightly lower for disposable income than for market income.
The impact of taxes and transfers is somewhat larger for the variance of permanent shocks.
Early in life, the permanent shocks to market income of high skilled are attenuated
substantially, although they remain large. Toward the end of the life-cycle, the
tax–transfer system reduces the magnitude of the permanent shocks somewhat. Taken
together, our results suggest that the redistributive nature of the Norwegian tax–transfer
system plays a key role in attenuating the magnitude and persistence of income shocks,
especially among the low educated. This finding could have important implications for
consumption inequality and the overall ability of families to insure labor income shocks.
Economic theory predicts that consumption responds strongly to permanent shocks, and
empirical evidence suggests little if any self-insurance in response to permanent shocks
among individuals with no college education (see e.g. Blundell et al., 2008).

<hs>  Family income</hs>
  ~~~~~~~~~~~~~

We now shift attention to examining whether the addition of income from the spouse offsets
or enhances labor market shocks. There are competing forces at play when going from
individual to family income (see e.g. Blundell et al., 2012). The first is that the
variance of market income is relatively large among females, reflecting considerable
dispersion in hours worked. The second is that the stochastic components of labor income
processes are likely to be correlated across spouses. If spouses were adopting perfect
risk sharing mechanisms, they would select jobs where shocks are negatively correlated.
Alternatively, assortative mating can imply that spouses work in similar jobs, similar
industries, and even in the same firm; as a consequence, their shocks could be positively
correlated. The third is that family labor supply is a possible insurance mechanism to
market income shocks. For example, the wife's labor supply could increases in response to
negative income shocks faced by the husband (see e.g. Lundberg, 1985). By comparing the
dynamics of individual and family income over the life cycle, we are able to assess the
overall impact of these three factors, but not identify the individual contribution of
each factor.17 Figs. 3 and 4 display the age profiles in the variances of transitory and
permanent shocks to family disposable income. By comparing these profiles to the ones for
individual disposable income, we can see that the magnitude of the shocks change little
when we add the income of the spouse. This suggests that risk sharing through (negative)
assortative mating or labor supply offset the high variance in income of wives and any
positively correlated shocks. Table 1 shows that permanent shocks remain highly persistent
for low and medium skilled, while falling for the high skilled when we add spouse's
income. We can further see that the persistence of transitory shocks change little when
including the income of the spouse.18

<h>INVESTIGATION OF INCOME PROCESSES</h>
---------------------------------

This section takes advantage of the size and detailed nature of the Norwegian data and
brings new evidence on several issues pertinent to the modeling of income processes.

<hs>  Nonstationarity in age and time</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our rich panel data allows us to let the variances components depend on age in an
unrestricted way, while controlling flexibly for calendar time effects. This raises
questions such as: What is missed by the standard specification in the literature with
age-independent variance components? How important is it to account for calendar time
effects such as the business cycle or tax reforms? Appendix Table C.1 investigates the
implications of assuming age-independent shocks. We display the parameter estimates from a
model in which the variances of the error components in Eq. (1) are restricted to be
constant across the life cycle. For the high skilled, the estimated persistence parameter
falls from almost one with age-dependent variance of shocks to .75 with age-independent
variance of shocks. By comparison, the age-independent specification does not affect the
estimates of the persistence parameter for the low and medium skilled. Figs. 5 and 6 show
the misspecification bias from restricting the variances of transitory and permanent
shocks to be constant over the life cycle. These figures highlight the importance of
allowing for age nonstationarity to capture the labor income dynamics of low and high
skilled workers. What features of the data give rise to the misspecification bias we
observe? Recall that high skilled have a U-shaped age profile in the variance of
individual market income. We argue that targeting these moments with an age stationary
model puts a downward pressure on ρ. With a persistent parameter close to one, it becomes
difficult to match the U-shaped profile with an age-independent specification because the
permanent shocks would then accumulate over the life cycle, generating an increasing and
convex profile in the variance of individual market income. In Fig. 7, we illustrate the
importance of allowing for time nonstationarity to get a clear picture of the typical
income dynamics over the life cycle. We estimate the model given in (1) separately by
cohort, and graph the age profiles in the variance of transitory shocks to disposable
income for different cohorts; for brevity, we do not split the sample by education. The 5
year interval between the cohorts allows us to clearly see the impact of a tax reform: For
each cohort, we observe a spike in the variance of transitory shocks at that the time of
the change in tax policy.19 By comparison, our baseline results control for such calendar
time effects by averaging the moments across the cohorts before estimating the income
process. After taking out calendar time effects, the variance of transitory shocks
exhibits a smooth and decreasing profile over the life-cycle.

<hs>  Heterogeneous profiles</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

Our findings suggest important heterogeneity in labor income dynamics by age, skill level,
and their interaction. This raises questions such as: What happens if we do not allow for
the possibility that individuals with different education levels face different income
processes at the variance level? How important is it to allow for unobserved heterogeneity
in the income growth rates within skill groups? Appendix Table C.2 displays parameter
estimates from the baseline model of income dynamics when we do not split the sample by
education. The persistence parameter in the pooled sample is one, suggesting that the
shocks to (log) labor income can still be described as the sum of a transitory shock and a
highly persistent process. Figs. C.8 and C.9 show the age profiles in the variances of
shocks when we restrict the income processes at the variance level to be the same across
skill groups. Because the results from the pooled sample mix the income processes of low
and high skilled, we obtain an inverse U-shaped age profile in the variances of permanent
shocks. However, this pattern is at odds with the age profiles of both high and low
skilled: While the former group experience large permanent shocks early in life, the
latter group faces the largest shocks at older ages. These findings point to the
importance of allowing for heterogeneity by education levels to capture the labor income
dynamics of young and old workers. So far, we have imposed homogenous experience profiles
(i.e. βi = 0) within each skill group. We now relax this assumption and allow for a linear
experience profile in the model given by Eq. (1). Appendix Table C.3 displays the
parameter estimates for individual market income, while Figs. 5 and 6 show the
misspecification bias from imposing homogenous experience profiles. The results suggest
education levels do a good job in capturing heterogeneity in the dynamics of labor income
over the life-cycle. Only for the high skilled, there is evidence of significant
unobserved heterogeneity in the income growth rates; accounting for this heterogeneity
lowers the persistent parameter from .98 to .90, but barely moves the age profiles in the
variances of permanent and transitory shocks. Appendix Fig. C.12 illustrates the
heterogeneity in market income profiles for the high skilled. There is a non-negligible
fanning out of the income profiles. At the same time, there is a negative correlation
between the initial conditions and the individual-specific income growth rate. This means
that high skilled workers with relatively low market income at age 25 (the initial age)
tend to have stronger income growth over the life cycle, offsetting some of the fanning
out displayed in Fig. C.12.

<hs>  Serially correlated transitory shocks</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Because we have long panel of individuals, we can separately identify a transitory process
with serially correlated shocks and a permanent process which allows for a persistence
parameter less than unity. In many cases, however, this is difficult because the panel of
individuals is too short (or plagued by problems such as attrition and small sample
sizes). In Figs. 5 and 6, we examine the implications of restricting the transitory
component in the model given by Eq. (1) to be uncorrelated over time. In the simple case
of serially uncorrelated transitory shocks, all the persistence in the income data is
attributed to the permanent income component. By comparison, the transitory component is
assigned a larger share of the total variance in our baseline model, because the process
captures short-duration persistence in the data. However, our estimates suggest the
misspecification bias from assuming serially uncorrelated transitory shocks is relatively
small compared to the biases from ignoring heterogeneity in labor income dynamics by age
and skill level.

<h>CONCLUSION</h>
----------

What do labor income dynamics look like over the life-cycle? What is the relative
importance of persistent shocks, transitory shocks and idiosyncratic trends? To what
extent do taxes, transfers and the family attenuate these various factors in the evolution
of life-cycle inequality? In this paper, we used rich Norwegian panel data to answer these
important questions. We estimated a process for income dynamics that allows for key
aspects in the evolution of labor income over the life-cycle, including non-stationarity
in age and time, shocks of varying persistence, and heterogeneous profiles. Our estimates
of the labor income dynamics of males showed that the magnitude of permanent and
transitory shocks varies systematically over the life-cycle, and that there is essential
heterogeneity in the variances of these shocks across skill groups. We found that the
redistributive nature of the Norwegian tax–transfer system plays a key role in attenuating
the magnitude and persistence of income shocks, especially among the low skilled. Spouse's
labor market income, on the other hand, matters less for the dynamics of inequality over
the life-cycle. The size and detailed nature of the data we are using also allowed us to
bring new evidence on several additional issues pertinent to modeling of income processes.
One key finding was that restricting the age and time dependence of the variance of income
shocks can lead to quite misleading conclusions about the income process. Another key
finding was that allowing for heterogeneity by education levels is necessary to capture
the labor income dynamics of young and old workers. By way of comparison, the dynamics of
income over the life-cycle change little when restricting the transitory shocks to be
uncorrelated over time or allowing for heterogeneous experience profiles within each skill
group. Indeed, only for the high skilled, there is evidence of significant unobserved
heterogeneity in the income growth rates. Accounting for this heterogeneity lowers the
persistence of permanent shocks somewhat, but barely moves the age profiles in the
variances of permanent and transitory shocks.


<h>REFERENCES</h>
----------

  [2] Michael Baker, Gary Solon. Earnings Dynamics and Inequality among Canadian Men, 1976-1992: Evidence from Longitudinal Income Tax Records. doi:10.1086/345559
  [3] Richard Blundell, Luigi Pistaferri, Ian Preston. Consumption inequality and partial insurance. doi:10.1257/aer.98.5.1887
  [5] Jason Debacker, Bradley Heim, Vasia Panousi, Shanthi Ramnath, Ivan Vidangos. Rising inequality: Transitory or persistent? New evidence from a panel of U.S. tax returns. doi:10.1353/eca.2013.0004
  [6] Pierre Olivier Gourinchas, Jonathan A. Parker. Consumption over the life cycle. doi:10.1111/1468-0262.00269
  [7] Jonathan Heathcote, Kjetil Storesletten, Giovanni L. Violante. Two views of inequality over the life cycle
  [8] Mark Huggett, Gustavo Ventura, Amir Yaron. Sources of lifetime inequality. doi:10.1257/aer.101.7.2923
  [10] Costas Meghir, Luigi Pistaferri. Earnings, Consumption and life cycle choices. doi:10.1016/S0169-7218(11)02407-5
  [12] Kjetil Storesletten, Chris I. Telmer, Amir Yaron. The welfare cost of business cycles revisited: Finite lives and cyclical variation in idiosyncratic risk. doi:10.1016/S0014-2921(00)00101-X
  [13] Kjetil Storesletten, Chris I. Telmer, Amir Yaron. Cyclical dynamics in idiosyncratic labor market risk. doi:10.1086/383105
<ART>Learning to import from your peers
==================================

Authors: Márta Bisztray, Miklós Koren, Adam Szeidl
DOI: 10.1016/j.jinteco.2018.09.010
Year: 2018  |  Pages: 242-258
ASJC codes: 2002, 2003
Keywords: D22, F14, Imports, JEL codes:, Manager networks, Peer effects, R32, Social multiplier, Spatial spillovers

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We use firm-level data from Hungary to estimate knowledge spillovers in importing through fine spatial and managerial networks. By identifying from variation in peers' import experience across source countries, by comparing the spillover from neighboring buildings with a cross-street placebo, and by exploiting plausibly exogenous firm moves, we obtain credible estimates and establish three results. (1) There are significant knowledge spillovers in both spatial and managerial networks. Having a peer which has imported from a particular country more than doubles the probability of starting to import from that country, but the effect quickly decays with distance. (2) Spillovers are heterogeneous: they are stronger when firms or peers are larger or more productive, and exhibit complementarities in firm and peer productivity. (3) The model-implied social multiplier is highly skewed, implying that targeting an import-encouragement policy to firms with many and productive neighbors can make it 26% more effective. These results highlight the benefit of firm clusters in facilitating the diffusion of business practices.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Imports have large positive effects on firm productivity (Amiti and Konings, 2007; Halpern
et al., 2015), yet there is much heterogeneity in similar firms' importing behavior. One
explanation for this heterogeneity is the presence of informal trade barriers, when
specific knowledge or a trusted partner is needed for a productive import relationship.
When informal barriers are active, importing may diffuse from firm to firm through
personal and business connections. Mion and Opromolla (2014), Mion et al. (2016),
Fernandes and Tang (2014) and Kamal and Sundaram (2016) document such diffusion for
exports, but at present we have limited evidence on the—equally important— import side of
the market.1,2 Are there knowledge spillovers in importing? If there are, what factors
facilitate or limit diffusion? The answers can shed light on the puzzling cross-firm
heterogeneity in importing and its productivity benefits; and can guide trade policy to
exploit indirect effects. In this paper we use firm-level data from Hungary to document
and analyze knowledge diffusion in importing. In doing so, we make three main
contributions. First, we develop a portfolio of empirical designs which rule out many
alternative explanations and help advance the identification of trade spillovers in
spatial and managerial networks. We address firm heterogeneity by identifying from source
country variation, exclude spatial omitted variables by exploiting the precise
neighborhood structure, and also use plausibly exogenous firm moves. We consistently find
significant spillover effects. Second, we investigate the factors associated with stronger
diffusion. We find that knowledge flows are stronger when firms or peers are larger or
more productive. Knowledge flows also exhibit complementarities in firm and peer
productivity, showing that positive sorting can increase the overall adoption of
importing. Third, we demonstrate in a counterfactual analysis how network density and
positive sorting combine to shape adoption patterns. We document that the model-implied
social multiplier of importing is highly skewed in the number and type of peers, implying
that import subsidies targeted at firms in buildings with many productive neighbors are
much more effective. In Section 2 we present our data. We use a firm-level panel that
contains rich information about Hungarian firms during 1993–2003. We combine three data
sources: the Hungarian firm register, balance sheet data from the National Tax and Customs
Administration, and trade data from the Hungarian Customs Statistics.3 The firm register
contains, for the full universe of Hungarian firms, the precise address of the firm, all
owners with their country of origin, and all firm officials with signing rights, as well
as changes over time. As a result, we can trace changes in spatial and ownership links and
the moves of people. The balance sheet data include additional information on the foreign
ownership share and the industry of firms. And the customs data contain annual export and
import flows at the HS6 product level for each firm, separately for each destination and
source country. Section 3 presents our first main contribution: the empirical strategy and
results on import spillovers. The key identification concern with estimating spillovers is
one common to studies of peer effects (Manski, 1993): that a firm and its peer's import
choices may be correlated for reasons unrelated to learning. For example, firms in a
particular industry may make correlated location and import decisions. We address this
endogeneity problem using two main research designs exploiting progressively narrower
sources of variation, in combination with placebo tests and sample definition choices that
rule out several omitted variables. Our first research design is a linear probability
model measuring the effect of peer firms'country-specific experience on a firm's decision
about starting to import from the same country. We implement this design by including
firm-year and country-year fixed effects, effectively exploiting variation within a firm
in a given year: we ask if having a peer which has past experience with a given country
increases the probability of starting to import from that country, rather than from
another country. To increase comparability we only look at four source countries similar
in terms of imports: the Czech Republic, Slovakia, Romania, and Russia. And to ensure that
all firms are the same distance from the border we only consider firms located in
Budapest. We use this research design to estimate knowledge diffusion in two networks:
close spatial neighborhoods and managerial networks. Within spatial neighborhoods we
consider three types of peers: firms in the same building, firms in the two neighboring
buildings, and, as a placebo, firms in the two closest cross-street buildings. In
managerial networks, we define peers as firms from which an official with signing rights
has moved to the firm of interest. To limit confounding effects we always exclude
ownership-connected firms—defined as those which share an ultimate owner with the firm of
interest—from the spatial and managerial peer groups. Our first design yields significant
positive import diffusion estimates in both networks. For neighborhood networks we
document highly spatially localized spillovers. Having a same-building peer with import
experience from a specific country increases the probability of starting to import from
the same country by 0.2 percentage points, which roughly doubles the baseline probability
of starting to import from one of the four countries. The effect of a neighbor-building
peer's import experience is only one-fifth as large, indicating fast decay by distance.4
The placebo effect of a cross-street peer's import experience is insignificant and small.
Finally, in managerial networks the same design yields spillover estimates which are twice
as large as the same-building effect. This design addresses several omitted variable
problems which often plague estimates of knowledge diffusion. Most directly, by exploiting
variation across source countries it addresses the basic concern that importers tend to be
connected to other importers. Specifically, in the absence of source country variation the
firm-year fixed effects would soak up all the variation in peers' import experience.5 In
addition, our controls and placebo also address more subtle country-specific omitted
variables. In particular, by controlling for ownership links we remove omitted variables
based on joint ownership. Results below show evidence on diffusion across industries,
addressing concerns with same-industry clustering. And, most important, the neighboring
building versus cross-street building comparison rules out any remaining omitted variable
as long as knowledge spillovers decay faster than the spatial correlation in that
variable. One remaining concern with our first design is that it does not make explicit
the source of variation in peer firms' experience, and therefore it may be subject to some
unspecified—highly spatially concentrated—omitted variable. In our second design we
address this problem by exploiting a concrete plausibly exogenous source of variation:
firm moves. We conduct an event study of the impact of firms with country-specific import
experience moving into an address where no such experience was present earlier. The move
is a positive shock to local country-specific knowledge. We show that firms located in
such an address start to import from the country known by the mover with a higher
probability than from other countries, relative to firms in addresses where the mover had
no such experience. Consistent with the logic of diffusion, the response of imports to the
move is gradual. The magnitude of the estimate is comparable to that of our first research
design. The consistency of the results identified in different networks and from
increasingly narrow sources of variation further supports the knowledge spillovers
interpretation. In Section 4 we present our second main contribution: the heterogeneity of
the spillover effect. We explore heterogeneity both to internally validate our estimates
and to obtain lessons about mechanisms. We measure heterogeneous effects both by the
characteristics of the firm and those of the peer, as well as their interactions. Focusing
on same-building peers, we find that larger, more productive and foreign-owned firms
benefit more from peers' import experience. Firms also learn more from peers which are
larger, more productive or foreign-owned. And spillovers are also stronger when more peers
have import knowledge. These results are all consistent with the knowledge diffusion
interpretation: better firms are likely to be both more receptive to information and more
effective in passing it on, and multiple sources should further increase the rate of
diffusion.6 We then document that the strength of the spillover also exhibits
complementarities between the firm's and the peer's characteristics. We show that high-
productivity firms tend to learn even more from higher-productivity peers than low-
productivity firms do. Similarly, we show that the effect of peers operating in the same
industry or importing the same product category is significantly larger than that of other
peers. At the same time, spillovers from peers operating in different industries or
importing different product types are still significant. The results on complementarities
are potentially relevant because they suggest that positive sorting—even holding fixed the
network structure—can generate aggregate gains in importing. In Section 5 we present our
third main contribution: a counterfactual analysis to assess the policy implications of
the estimated import spillover effect. Our results so far imply that spillovers should be
stronger when (i) the number, and (ii) the productivity of experienced peers is higher. To
quantitatively evaluate the combined impact of these forces, we compute the model-implied
social multiplier effect on imports of a firm entering into an import market, which
incorporates spillovers over the next five years. We calculate the multiplier using the
same-building estimate which accounts for heterogeneity by the productivity of the firm
and its peers, and also allows for an increase in spillovers with the number of
experienced peers. Because the number and productivity of peers varies across the sample,
we obtain a separate multiplier for each firm which has not imported yet from one of the
four countries. The results show substantial skewness in the social multiplier. In
particular, we find that the five-year social multiplier is 1.03 for the median firm and
1.13 for the firm in the 90th percentile. Thus, while accounting for spillovers is not
important for the typical firm, it is potentially quite important for a substantial share
of firms. An implication is that there may be significant gains from targeting trade
policies. We confirm this by showing that a targeted import subsidy policy treating firms
for which spillover effects are the largest can be 26% more effective than a non-targeted
one. Because finding the firms with the highest expected indirect treatment effect only
requires public information on firms' balance sheet and address, this targeting is in
principle directly implementable. Our result quantifies the benefit of clusters—especially
of firms with high productivity—in facilitating the diffusion of good business practices.
We build on a literature on knowledge spillovers in trade, most of which studies the
diffusion of exporting. An important part of the literature explores spatial spillovers.
Early work focused on the diffusion of the decision to export, and obtained mixed
results.7 More recent work studies the diffusion of specific knowledge, such as export
experience with a particular country or product, and generally finds evidence for
spillovers (Koenig, 2009; Koenig et al., 2010; Poncet and Mayneris, 2013; Castillo and
Silvente, 2011; Ramos and Moral-Benito, 2013; Mayneris and Poncet, 2015). Using uniquely
rich data on trade partners Kamal and Sundaram (2016) document the diffusion of concrete
export partners. And Fernandes and Tang (2014) document export spillovers using for
guidance a formal model that allows them to test specific predictions of the learning
hypothesis. All these papers define spatial neighborhoods to be cities or similarly large
agglomerations. Our spatial spillover results improve identification by using
substantially more precise measures of neighborhoods. When networking benefits decay
rapidly in space (Arzaghi and Henderson, 2008), spatial networks should be measured at a
fine resolution to avoid confounding variation from omitted spatially correlated
variables. Our results show that spillovers do decay fast, highlighting the relevance of
our precise measures. More broadly, we also contribute to this literature by our focus on
imports, our analysis of heterogeneous effects and the implications for targeted trade
policies. Another part of the export spillovers literature studies spillovers through
managerial moves. These papers show that having a manager with prior export experience
join the firm increases the likelihood that the firm starts to export (Choquette and
Meinen, 2015; Mion and Opromolla, 2014; Mion et al., 2016; Sala and Yalcin, 2015; Masso et
al., 2015). We contribute to this work by focusing on import spillovers; by having a
comprehensive study in which we compare spillovers in managerial networks to spillovers in
spatial networks; and by our analysis of heterogeneous effects and the implications for
targeted policies. Given this existing work on export spillovers, our main focus in this
paper is the more novel and equally important topic of import spillovers. There is almost
no work on this topic, the sole exceptions—to our knowledge—being Harasztosi (2011) and
Harasztosi (2013), which estimate import spillovers in Hungarian NUTS4 agglomeration
units. Our contribution to this work is the use of more precise neighborhood definitions,
a variety of empirical designs that limit confounding factors, a more comprehensive
analysis of multiple networks, the results on heterogeneous effects, and the policy
counterfactual analysis. Finally, we build on a literature on firm networks and diffusion
in networks. Chaney (2014) develops a model in which firms can acquire trading partners
through existing contacts; Fafchamps and Quinn (2015) and Cai and Szeidl (2018) show that
managerial meetings can facilitate the diffusion of business relevant information; and
Banerjee et al. (2013) explore network-based targeting of microfinance in the presence of
knowledge diffusion. Our study documents and analyzes these sort of network effects in the
novel and important context of import spillovers.

<hs>  Data sources</hs>
  ~~~~~~~~~~~~

We create our panel of Hungarian importers by combining data from three sources.

        Firm registry 1993–2003

        Data from the Hungarian Company Register contain basic information for the full
        universe of Hungarian firms, including the firm's name, tax identifier, and
        precise address: zip code, city, street, number, floor and door number. These
        variables have associated start and end dates, allowing us to track firm moves
        over time. The registry data also contain information about the firm's owners, and
        officials with signing rights which include directors, board members, the CEO, and
        some employees. As the employees with signing rights are usually at or near the
        top of the firm hierarchy, we sometimes—slightly imprecisely—refer to these people
        as managers. For firm owners the data contain the name and registry number; and
        for person owners and officials the name, mother's name and home address. These
        records also have start and end dates. We use the name, mother's name and address
        to create an anonymous unique identifier for each individual in the data. We use
        this identifier to track individuals across firms and over time. Our method allows
        for typos and slight variations in names, such as omitting the middle name.

        Balance sheets 1993–2003

        We have balance sheet data for all double-bookkeeping Hungarian firms from the
        National Tax and Customs Administration of Hungary. These data also include the
        firm's industry at the 2-digitNACE level (Revision 1.1), and the shares of its
        capital owned by foreign entities, domestic private entities, and the Hungarian
        state.

        International trade 1993–2003

        Detailed firm-level trade data come from the Hungarian Customs Statistics. These
        data contain yearly exports and imports by each firm to and from each foreign
        country at the Harmonized System (HS) 6-digit product category. The reason that
        our sample period ends in 2003 is that the firm-level trade data are not available
        for later years. We use unique firm identifiers to link these three datasets.

     <hss>Firm sample</hss>

        We focus on imports from four countries that are comparable in terms of their
        exports to Hungarian firms: the Czech Republic, Slovakia, Romania and Russia. To
        avoid variation in distance from the border, we use only firms with headquarters
        in Budapest, which account for over 20% of all the firms in Hungary. Accordingly,
        when a firm moves its headquarters out of Budapest, we let it exit from our
        sample. These exclusions result in our main firm sample which contains 211,598
        firms and 1,189,402 firm-year observations. We conduct most of the analysis using
        our analysis sample, a (firm, source country, year) panel derived from our main
        firm sample. In this three-way panel we only include observations in which a firm
        in the main sample has not yet imported from the given source country up until the
        previous year. This sample construction allows us to estimate the probability that
        a firm starts to import from a particular country for the first time. We also make
        three additional exclusions. (1) We exclude firms for which the headquarters'
        address is missing, because for them we cannot define spatial networks. (2) We
        exclude firms which have >50 same-building peers to ensure that our results are
        not driven by large hubs. (3) We start the data in 1994 because separate trade
        data for the Czech Republic and Slovakia are only available starting 1993 and the
        analysis sample requires importer status of peers in the previous year.8,9 After
        these exclusions, the analysis sample contains 88% of the firms in the main firm
        sample and has 3,778,517 firm-year-country observations. About 5% of the firms in
        the main sample import from at least one of the four countries at least in one
        year during 1993–2003.

     <hss>Variable definitions</hss>

        We define the firm to have import experience with a country in a year if it has
        imported from that country in that year or in a previous year. This definition
        captures the idea that the firm has acquired import experience specific to that
        country by that year. We define experience with exports or with foreign owners in
        an analogous way. We classify a firm as foreign-owned in a year if it had majority
        foreign ownership that year. We classify imported products by their purpose using
        the Broad Economic Categories (BEC) classification. We create four product
        categories: Consumer goods (BEC 1, 6), Industrial supplies (BEC 2, 3), Capital
        goods (BEC 41, 51, 52) and Parts and accessories (BEC 42, 53). Using the Levinsohn
        and Petrin (2003) methodology we estimate from the balance sheet data total factor
        productivity (TFP) for each firm in each year, assuming a Cobb-Douglas revenue
        production function with capital and labor as factors and materials as an input,
        allowing coefficients to vary by two-digit industries. We normalize log
        productivity within each 2-digit industry to have mean zero in our main firm
        sample. We then assign firms to productivity quartiles in each year t, based on
        the average of their yearly 2-digit-industry-specific productivity percentile over
        the years t − 2, t − 1 and t. Taking the average over three years reduces noise,
        and results in a smooth but time-varying productivity index.

<hs>  Firm networks</hs>
  ~~~~~~~~~~~~~

A key ingredient in our analysis is data on peers in firm networks. We work with three
classes of peers, defined based on spatial, personal and ownership connections.

     <hss>Spatial peers</hss>

        We use a highly localized definition of spatial connections. We create three
        different spatial peer groups. (i) Same-building peers, defined as firms with the
        same street address up to building number. (ii) Neighbor-building peers, defined
        for a firm with building number n as firms in buildings in the same street with
        numbers n − 2 and n + 2.10 (iii) Cross-street peers, defined as firms in buildings
        in the same street numbered n − 1 and n + 1. From all three peer groups we exclude
        firms which have an ownership link—as defined below—to the firm of interest in the
        given year. Because the address data has dates, all these peer groups are year
        specific.

     <hss>Person-connected peers</hss>

        We define a firm B to be a person-connected peer of firm A in year t if some
        person X is an official with signing rights of firm A in year t and was an
        official with signing rights of firm B at some earlier date. We will often focus
        on person connections that can transmit import experience with some country c,
        which happens when firm B had import experience with c before person X left that
        firm. In all person-connected definitions we exclude people with signing rights
        who are liquidators—officials assigned to handle liquidation of the company—as
        well as people who are officials or owners of >15 firms in the given year. We also
        exclude from the set of person-connected peers firms which are likely to have
        shared decision makers with the firm of interest: those ever connected to the firm
        through ownership links (as defined below), and those that have the exact same
        address including floor and door number. But we do include peer firms which are
        located outside Budapest. With slight imprecision, we sometimes refer to the
        person-connected network defined this way as the managerial network.

     <hss>Ownership-connected peers</hss>

        We classify firms A and B to be linked by ownership in year t if they have a
        common ultimate owner. This includes two types of connections: (1) when A and B
        have a direct or indirect common owner; (2) when one of the firms is a direct or
        indirect owner of the other. We also include peers located outside Budapest in the
        ownership-connected peer group of a firm.

<hs>  Summary statistics</hs>
  ~~~~~~~~~~~~~~~~~~

Table 1 presents descriptive statistics on the firms in our main sample. The first column
refers to all firms in all years, the second column to firms in years in which they have
already had import experience from one of our four source countries, and the remaining
columns to firms with import experience from specific countries. Comparing between columns
1 and 2 shows that importers are on average older, larger, more likely to be foreign
owned, more likely to export, and have higher productivity than the industry average.
These patterns are familiar (Bernard et al., 2009). The remaining columns show that
importers from the four countries of interest are fairly similar in terms of all the
variables in the table, consistent with our intuition that these source countries are
roughly similar in terms of their associated import barriers. Table 2 shows the number of
firms and importers over time during our sample period. The rapid increase in the number
of firms is likely due to the development of the capitalist economy in the 1990s. And the
increase in the number of importers is probably a consequence of several factors: more
firms, lower formal trade barriers, and a country more deeply embedded in the
international economy. The considerable increase in importing shown in the table is a key
source of variation for our analysis below. Table 3 reports the distribution of degree
(number of peers) in the different firm networks. The average degree—shown in the bottom
row—is the highest for the same-building network (8.4) and the lowest for the the person-
connected network (0.3). The neighbor-building and cross-street networks are between these
two extremes (average degrees of 5.2 and 3.3) and although the latter is more sparse, have
a roughly similar degree distribution. In all networks a substantial share of firms are
isolated, i.e. have zero neighbors. This heterogeneity in degree across firms is one key
reason for our finding below that targeting import subsidy policies can substantially
increase their effectiveness.11

<h>ESTIMATING IMPORT SPILLOVERS</h>
----------------------------

This section presents our empirical strategy and results on the effect of peers'
experience on a firm's import decision. Our main hypothesis is that importing requires
source-country specific knowledge, which in turn diffuses in various firm networks. As a
result, we predict that firms which—other things equal—have peers with experience
importing from a particular country are more likely to start importing from that country.
We divide this section into four parts. We begin by presenting motivating evidence which
highlights a key component of the logic for identification: variation in peers' import
experience across different source countries. We then present two empirical designs. The
first design directly exploits this source country variation, and yields spillover
estimates in both spatial and managerial networks as well as placebo estimates that
confirm the logic of identification. The second design further improves identification for
spillovers in spatial networks by exploiting plausibly exogenous firm moves. In the final
part we assess the magnitude of our spillover estimates.

<hs>  Motivating evidence</hs>
  ~~~~~~~~~~~~~~~~~~~

Table 4 shows how we exploit source country variation in peers' import experience. The
table reports the probability of a firm starting to import from a particular country in a
year, conditional on it starting to import from one of the four countries that year, and
conditional on different importing patterns of its peers. The four panels correspond to
peers defined by the same-building, neighbor-building, person-connected and ownership-
connected networks. Within each panel, the top row shows the share of firms which start to
import from a country c, while the bottom row shows the share which start to import from a
different country.12 The left column computes this share for firms with peers that have
import experience with c but not the other countries; and the right column for firms with
peers that have import experience with a different country but not c. We report the
average share when c runs across the four countries, weighted by the number of
observations per country. The table shows that in each network, the share of firms
starting to import from country c is always higher when peers have c experience than when
peers have non-c experience. This fact suggests that peers' experience influences firms'
import decisions and forms the basis for our identification strategy. We now turn to more
fully develop this empirical approach and derive statistical inference, explicitly address
confounds, conduct placebo analysis and incorporate additional plausibly exogenous
variation.

<hs>  Research design 1: Peers'country-specific import experience</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Here i indexes firms, c indexes source countries and t indexes years, thus each
observation is a (firm, source country, year) triplet. We estimate the regression in our
analysis sample, which contains observations where firm i has not yet imported from
country c before year t. The left-hand-side variable Yict is an indicator for i importing
from country c in year t. Given that the sample excludes prior importers from c, Yict
measures entry into importing from c. On the right-hand side we include indicators for the
presence of country-specific import experience in various peer groups n. Specifically,
Xnic, t−1 is and indicator which equals one if there is at least one firm in firm i‘s peer
group n in year t − 1 which has import experience from country c at time t − 1, that is,
which imported from c in t − 1 or earlier.13 We use lagged peer experience because we
expect information diffusion to take time. We consider the five different peer groups (n)
defined in Section 2.3 above: (1) firms in the same building; (2) firms in the two
neighboring buildings, (3) firms in the two cross-street buildings; (4) person-connected
peers; and (5) firms in the same ownership network. Finally, αit denotes firm-year fixed
effects, μct denotes country-year fixed effects, and εict represents other sources of
variation in importing. Our main hypothesis is that, due to knowledge spillovers, βn > 0
for the spatial and managerial networks. We also expect βn > 0 for the ownership network,
but in that network the mechanism need not be a spillover: it is also possible that the
common owner's knowledge causes firms in the network to import from the same country.
Because they play an important role in identifying our key coefficients, it is useful to
discuss the fixed effects in Eq. (1). The firm-year fixed effects αit control for any
omitted variable driving import behavior which is specific to the given firm in the given
year. This is a rich set of fixed effects, and the only reason it can be included is
because the data have an additional panel dimension: multiple source countries. In
particular, estimating Eq. (1) in the absence of data on source countries, or with a
single source country, would not be feasible because the firm-year fixed effects would
soak up all the variation in the dependent variable. In this sense the key βn coefficients
are identified from source country variation. An implication is that standard firm
controls, such as sales, employment, ownership status, or other balance sheet variables
need not be included in the regression, since they are already picked up by the firm-year
effects. In turn, the second set of fixed effects μct pick up country-year specific
variation, for example business cycle fluctuations in a source country that might affect
the supply of imports. Due to their presence, we do not need to include country-specific
controls such as the exchange rate or GDP of the source country. Beyond import spillovers,
slightly modified versions of Eq. (1) can also be used to estimate other kinds of
spillovers. We will look at cross-activity spillovers where on the right-hand side of the
equation we measure peer firms'country-specific experience in a different domain, such as
exporting to or having a foreign owner from the country; and (in Appendix A.2) we will
also use a variant to present evidence on export spillovers.

     <hss>Identification</hss>

        Since Eq. (1) is essentially a peer effects regression, the main threats to
        identification are those highlighted by Manski (1993): endogenous peer groups and
        correlated omitted variables.14 Endogenous peer groups might arise because of
        clustering or because of peer choice. An example in the spatial network is when
        firms from one industry, or “high-type” firms, tend to both co-locate and make
        similar import decisions, creating spurious correlation between Xnic, t−1 and
        εict. An example in the managerial network is when a firm hires a manager because
        of her or his import knowledge. And an example of correlated omitted variables is
        when particular physical locations are better for importing from a country c,
        perhaps because they are close to c. Our first research design addresses these
        concerns in three main ways. (1) Source-country variation. By using this variation
        we address the basic concern that importers tend to be connected to other
        importers. As discussed above, if we were to estimate Eq. (1) ignoring the source
        of imports, the firm-year fixed effects αit would soak up all the variation. The
        implication is that remaining threats to identification must be based on country
        variation: for example, if certain types of firms tend to import from certain
        countries and co-locate with each other. (2) Sample definition. We use comparable
        source countries; firms based in Budapest; and we omit ownership-based links from
        the spatial and managerial networks. Our sample choices mitigate several concerns.
        Because the source countries are similar, it is less likely that “high-type” firms
        import from one, while “low-type” firms import from another. Because all firms are
        in Budapest, omitted variables based on distance from a country are muted. And by
        removing ownership links we address the concern that correlated decisions may be
        driven by a common owner. In addition, by focusing on imports we limit the concern
        of endogenous manager choice as knowledge of importing seems less likely to be a
        driver of hires than for example knowledge of exporting would be. (3) Placebo
        spatial peers. Perhaps the most convincing component of our design is that by
        exploiting the fine spatial structure we can compare same-building and neighbor-
        building spillovers with a cross-street “placebo spillover”. As long as spillovers
        are more spatially concentrated than the omitted variables—an assumption
        consistent with the results of Arzaghi and Henderson (2008)—estimating higher β
        coefficients for the closer spatial peers is evidence for knowledge diffusion. For
        the above reasons we feel that the most plausible confounds are accounted for by
        our current research design. Still, a possible concern is that, because the design
        does not make explicit the source of variation in peer firms' experience, it may
        be subject to some remaining—highly spatially concentrated—omitted variable. In
        the next subsection we address this concern by combining the current design with
        plausibly exogenous variation in peer firms' experience due to firm moves.
        Although that approach requires weaker identification assumptions, it can only be
        used to estimate spillovers in spatial networks. We therefore begin the analysis
        with the current design to demonstrate that knowledge spillovers about imports are
        present quite broadly across different types of networks.

     <hss>Results</hss>

        Table 5 reports estimates of regression (1). In this and all subsequent tables
        reporting regression results, coefficients are measured in percentage points. To
        account for spatial correlation in the error term, in all specifications we
        cluster standard errors by building. Column 1 focuses on spatial spillovers. The
        estimated effect of having a same-building peer with country-specific import
        experience is a significant 0.22. Intuitively, having a peer with experience
        importing from a particular country, e.g., Slovakia, increases the probability
        that the firm starts to import from that country by 0.22 percentage points. For
        comparison, the baseline probability that a firm starts to import from a specific
        country is 0.19%; thus having a peer with experience importing from a country more
        than doubles the probability of entering that import market. Column 1 also reports
        that the estimated effect of having a peer with country-specific import experience
        in a neighboring building is a significant 0.04. This is a fifth as large as the
        same-building effect, and shows that while spillovers to neighboring buildings are
        also present, their intensity declines rapidly with distance. The cross-street
        spillover effect is an even smaller and insignificant 0.03. This result lends
        support to our identification strategy: if a spatially correlated omitted variable
        was driving our estimates, we would expect that variable to also affect firms in
        buildings across the street. Taken together, these estimates strongly support the
        presence of spatial spillovers in importing. Column 2 reports the analogous
        estimate for the person-connected networks. Having a firm official who had prior
        experience importing from a country increases the probability of importing by a
        significant 0.43, or almost half a percentage point. This estimate is twice as
        large as the same-building spillover effect. The larger magnitude seems intuitive:
        same-building diffusion is likely to be more limited because interactions between
        members of different firms are probably less common and less intense. In contrast,
        for person-connected spillovers, interactions are almost guaranteed since the
        manager now works for the firm. Column 3 shows the analogous estimates in the
        ownership-connected network. Here we estimate an even larger coefficient of 0.53.
        Importantly, this coefficient cannot be interpreted as a knowledge spillover
        because it is likely partly driven by a common owner making sequential import
        decisions for her or his firms. Indeed, the reason we include this specification
        is to show that controlling for the common ownership channel—which we do by
        excluding ownership-connected firms from the other networks—is important to
        convincingly document knowledge spillovers in spatial and managerial networks.
        Column 4 shows that combining all three types of networks in the same
        specification leaves the estimates essentially unchanged, indicating that the
        different networks represent genuinely different spillovers. We conclude that
        there are significant import spillovers in both spatial and managerial networks.
        In Appendix A.1 we show that these results are also robust to a range of
        specification changes including various subsamples (Table A1, A3), additional
        controls for the firms' or its peers'country-specific experiences (Table A1) and
        different measures of connections (Table A2).

<hs>  Research design 2: peer moves</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In our second research design we exploit a specific, plausibly exogenous source of
variation in peer knowledge, which is created by firm moves. Focusing on the same-building
spillover, we explore the effect of a peer with particular import experience moving into
the building on a firm's subsequent import decision. This design has power because moves
are quite frequent, with >25% of the firms in our main sample moving at least once.15 As
it is unlikely that the mover would internalize the effect of its import experience on
other firms in the building when it chooses its location, we can plausibly assume that
country-specific experience brought by the mover is an exogenous shock for the local
firms. Similarly, although the owner of the building might want to attract good firms, it
is less plausible that she would want to attract firms with specific import experience. We
estimate the impact of moves using an event study, in which the event is when a firm moves
from another address into a building. The sample consists of (i, c, t), that is, (firm,
source country, year) observations where firm i is located in a building in some year t
which is subsequent to some other firm j moving in the same building. The event is the
earliest date at which another firm moves into the building of i. To limit the confounding
effects of preexisting neighbors, we restrict the sample to observations in which no
incumbent firm in the building had import experience with the country c prior to the
event. We do not require that the mover firm j has import experience with the country c.
Buildings with movers having no import experience serve as controls. Here Yict is an
indicator for firm i having imported from country c in some year up to and including t.
Ditτ is an event-year indicator which equals one if the mover firm came to the building of
i exactly τ years before t; and the τ = 5 category also includes those observations in
which the move occurred >5 years ago. Xic is an indicator for the mover firm having had
import experience with country c by the time of the move. As before, αit and μct denote
firm-year and country-year fixed effects and εict denotes the error term. In this
specification the coefficients γτ measure the baseline dynamics of importing from a
country c following a move by any firm. The coefficients of interest are the βτ which
measure the additional gains in importing when the mover had prior experience with country
c. Because of the firm-year fixed effects, similarly to the previous research design this
regression is also identified from variation across source countries. Because Yict
indicates if the firm has ever imported from c by t, and because the sample definition
ensures that the i has not imported from c before the mover's arrival, Yict effectively
measures if a firm with no prior import experience starts to import from c in the period
between the arrival of the mover and t. Thus βτ captures the probability that the firm
learns how to import by year τ, even if that firm does not import in every subsequent
year. Fig. 1 presents visual evidence from the event study by plotting the estimates of βτ
together with their 95% confidence intervals. Panel (a) shows the results from the
specification without fixed effects, while Panel (b) from one that includes the full set
of fixed effects. Although the point estimates in the second specification are somewhat
lower and the standard errors wider because of the large increase in the number of
controls, both specifications show the same basic pattern: a gradual and eventually
significant increase in the probability of importing from a country subsequent to a new
neighbor with country-specific import experience moving in. The fact that the increase is
gradual is consistent with the idea of knowledge diffusion. In the more conservative fixed
effect specification of Panel (b), the insignificant first-year effect of 0.12 percentage
points increases to a significant 0.78 percentage points after four years.16 These
estimates have the same order of magnitude as the estimated same-building effect of 0.22
percentage points in research design 1, but highlight the importance of explicitly
considering the dynamic response to moves. The pattern revealed here serves as one
motivation for examining the dynamic response of further import entries to a new entry in
the counterfactual analysis of Section 5 below, where we will also be able to compare
explicitly the dynamics implied by research designs 1 and 2. In summary, our research
designs 1 and 2, exploiting different sources of variation, different networks, as well as
a placebo design, consistently yield evidence in support of the presence and economic
relevance of the knowledge diffusion hypothesis. We conclude that knowledge spillovers in
spatial and managerial networks play an important role in shaping firms' import decisions.

<hs>  Benchmarking magnitudes</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

To get a better sense of the magnitude of the spillover effect here we compare it to three
sets of benchmarks. As our first benchmark we use export spillovers, the existence of
which was documented by Mion and Opromolla (2014), Fernandes and Tang (2014) and Kamal and
Sundaram (2016) among others. To make this comparison meaningful, we use the same data and
empirical approach for both types of spillovers: we employ our identification strategy 1
to also estimate export spillovers in Hungary. Table A6 in Appendix A.2 presents the
results. Both the patterns and the magnitudes are similar to our import spillover results.
For example, in the full model including other type of experience as well the same-
building effect is 0.16 percentage points, the neighbor-building effect is 0.04 percentage
points and the managerial peer effect is 0.37 percentage points. Relative to the baseline
hazard of starting to export, 0.21, these estimates correspond to an increase in export
probability of 76%, 19% and 176%, while the analogous numbers for the increase in import
probability relative to its baseline of 0.19 are 116%, 21% and 216%. Export spillovers,
like import spillovers, are also highly concentrated in space. We conclude that diffusion
of knowledge about importing is about as strong as diffusion of knowledge about exporting.
As a second benchmark we ask what increase in firm productivity would predict the increase
in the probability of importing created by knowledge spillovers. In our sample the
probability of starting to import from a country is 0.19% for not-yet-importer firms in
the lowest productivity quartile,17 0.28% in the second quartile, 0.47% in the third
quartile and 0.58% in the highest quartile. Consequently, the estimated same-building
import spillover effect of 0.21 percentage points is comparable to the predicted increase
in the probability of starting to import as a firm moves from the second to the third
productivity quartile. This result further confirms the economic significance of the
estimated import spillover effect. In our third benchmark we look not at the strength of
the spillover but at its speed of decay in space. In particular, we infer a parameter of
spatial decay that can be explicitly compared to similar decay parameters in the
literature. Our approach is to convert the same-building and neighbor-building estimates
of research design 1 to a distance-based metric. We work with the decay function βij = k ⋅
e−δ⋅distij, where βij is the estimated spillover from firm j to i, distij is the spatial
distance between the two firms, and k and δ are parameters. In the 65% of the sample which
we were able to geocode, we find that the average distance between two neighboring
buildings is 28.1 m. Assuming that distance is zero if two firms are in the same building,
calibrating δ and k to the specification of column (4) in Table 5, we obtain δ = 0.0579/m.
This implies that spillovers decline by 5.6% every meter.18 This value is somewhat higher
than other estimates of within-city spatial decay. Indeed, the estimates of Arzaghi and
Henderson (2008) on networking benefits among advertising agencies in Manhattan imply a
decay of 0.3% per meter; those by Rossi-Hansberg et al. (2010) on housing externalities in
Richmond imply a decay of 0.2% per meter; and those by Ahlfeldt et al. (2015) on
production and residential externalities in Berlin imply decays of 0.4% respectively 1%
per meter.19 The main common feature of these results and ours is that they all represent
fairly strong decay: knowledge spillovers appear to be highly spatially concentrated. And
the fact that our estimate is the highest suggests that in our context building boundaries
are important barriers to diffusion. Our decay parameter estimate may be useful for
calibrating urban economics models that feature knowledge diffusion of business practices
such as importing.

<h>HETEROGENEITY AND MECHANISMS</h>
----------------------------

In this section we investigate the heterogeneity of import spillovers by firm and peer
characteristics. We focus on same-building spillovers because these were the strongest and
most cleanly identified. We first explore heterogeneous effects separately by firm and
peer characteristics, and then investigate how the interaction between these
characteristics influences the strength of diffusion. This analysis yields lessons about
the mechanism of spillovers, highlighting the potential benefits of clusters and targeted
policies, which we then quantitatively evaluate in the counterfactual analysis of Section
5.20

     <hss>Firm heterogeneity</hss>

        Here h indexes firm categories by a characteristic, such as productivity
        quartiles; and Iith is an indicator which equals one if firm i in period t is in
        the particular category h, such as the highest productivity quartile. The variable
        Xsb is an indicator for peers' import experience in the same building.
        Accordingly, the coefficients βh measure the effect of experienced same-building
        peers for firms in category h. For completeness, the controls include the
        analogous interactions of the category indicators with import experience in the
        four other networks (neighbor building, cross-street building, managerial and
        owner network).21 As usual, αit and μct denote firm-year and country-year fixed
        effects and εict denotes the error term. Table 6 reports the results from
        estimating heterogeneous effects by firm size, productivity and ownership. Column
        1 focuses on size measured as employment, and categorizes firms into four groups.
        Group 1 includes those firms with at most 5 employees, group 2 those with 6–20
        employees, group 3 those with 21–100 employees and group 4 includes firms with
        >100 employees.22 The coefficient of 0.07 percentage points shows significant
        spillover effects for the smallest firms in group 1. The subsequent coefficients
        imply that the spillover effects for larger firms are larger than those for firms
        in group 1, and are increasing in the firm's size category. t-tests show that the
        difference between the estimated coefficients of subsequent groups is significant
        at 5% in each case (denoted by # in the table). Larger firms are more likely to
        respond to import knowledge in their building. Column 2 reports heterogeneous
        effects by firm productivity quartile, defined using our TFP estimates introduced
        in Section 2. Here we find no spillovers for the least productive firms in group
        1, but significant and increasingly strong spillovers in the higher productivity
        quartiles. The coefficients of subsequent groups are significantly different in
        two of the three cases. Finally, in column 3 we look at ownership: group 1
        represents domestically-owned firms and firms without information on ownership,
        while group 2 represents foreign-owned firms. Spillovers are significant in both
        groups and significantly larger for foreign firms. Taken together, these results
        suggest that absorptive capacity (Lychagin, 2016), which is more likely to be
        present in larger, more productive, and foreign firms, is important for the
        adoption of import knowledge.

     <hss>Peer heterogeneity</hss>

        Here too we create categories for a characteristic, such as size, and Xsbic,
        t−1(h) is an indicator for having a same-building peer in category h which has
        import experience. Thus βh measures the effect of having an experienced peer in
        category h. Similar to Eq. (3) the controls include the analogous variables for
        the other networks. Table 7 reports the results. Column 1 shows spillovers by peer
        size, using the same cutoffs of 5, 20 and 100 employees already used above.23
        Spillovers are significant even from peers in the smallest group. Although the
        differences are not significant at 5%, the point estimates show that spillovers
        are larger when peers are larger, except for peers in the highest quartile where
        the coefficient is imprecisely estimated. Column 2 shows the analogous
        specification using peers' productivity quartiles. Here too, spillovers are always
        positive, and point estimates are larger for higher productivity peers. The
        difference between the third and fourth quartile is significant. Finally, column 3
        shows significant spillovers from domestic peers (group 1) and significantly
        larger spillovers from foreign peers (group 2). Although the coefficients in this
        table are slightly less precisely estimated, their general pattern strongly
        suggests that the import knowledge of larger, more productive and foreign
        firms—perhaps because they are more successful importers or more trusted peers—is
        more likely to diffuse. To further confirm this logic, in Table A7 of Appendix A.3
        we show that spillovers are stronger from “more successful” importer peers, where
        import success is measured with the persistence of the peer's import experience.

     <hss>Number of peers</hss>

        We next explore whether having more peers with country-specific import experience
        increases the probability of importing. Simple models of diffusion would predict
        such an effect, as with more informed peers there are more opportunities for
        learning. We consider a specification in which the effect is linear and use the
        number of peers with country-specific experience as a right-hand side variable.
        Column 1 of Table 8 shows that increasing the number of experienced peers in the
        same building by one increases the average probability of import entry by 0.2
        percentage points. Column 2 presents similar results from a more flexible
        specification in which we separately estimate the effect of having exactly k
        experienced peers in a specific peer group. These coefficients are comparable in
        magnitude to the 0.2 effect of the linear specification, and given the standard
        errors we cannot reject that in this range the number of experienced peers
        linearly increases the probability of importing. Taken together, the above results
        reveal plausible heterogeneity in knowledge spillovers: diffusion is stronger when
        firms are better, when peers are better, when the quality of knowledge is higher,
        and when there are more learning opportunities.

<hs>  Interaction between firm and peer characteristics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We turn to explore how firm and peer characteristics interact in shaping diffusion.
Interaction effects are potentially important because their presence indicates that
sorting firms can further increase the adoption of good business practices.

     <hss>Productivity complementarities</hss>

        Table 9 shows the results from estimating this regression. Column 1 reports a
        specification in which high productivity is defined as the top quartile in the
        productivity distribution. The fact that the coefficients of the non-interacted
        indicators of high-productivity firm (βhl) and high-productivity peer (βlh) are
        positive and significant is familiar from the previous subsection. The key novelty
        in the specification is that the coefficient of the interaction between high-
        productivity firm and high-productivity peer is a significant 0.5 percentage
        points. In column 2 we change the definition of the indicator for high-
        productivity firm to be above the median of the productivity distribution. The
        patterns obtained here are similar, and in particular the coefficient of the
        interaction continues to be significant and positive. From these results we
        conclude that there are statistically and economically significant
        complementarities between firm and peer productivity for the adoption of good
        business practices. One implication of these results concerns the benefits of
        sorting. Because of positive complementarities, sorting firms by productivity can
        generate aggregate gains in the overall adoption of good business practices. This
        force is distinct from the basic idea that having more informed peers increases
        adoption: it suggests that even holding fixed the average number of informed
        peers—that is, the neighborhood structure—changing the pattern of sorting can
        further increase adoption. Table 10 shows the results, using the top productivity
        quartile for the definition of high-productivity firms. The positive and
        significant coefficients show that spillovers are positive for any firm type and
        peer type, so that having more knowledgeable peers increases the probability of
        importing. And the fact that βhh is much larger than the other coefficients shows
        the complementarity effect: diffusion is stronger when both the firm and the peers
        are more productive.

     <hss>Same-industry and same-product effects</hss>

        To further explore the nature of complementarities, we investigate whether
        spillovers are larger between same-industry firms, and within a given imported
        product category. For same-industry effects our strategy is to include separate
        indicators for experienced peers operating in the same 2-digit industry as the
        observed firm and operating in different industries. We do this for all networks,
        but only report the results here for the same-building network. Column 1 of Table
        11 shows that same-building peers have a larger effect if they operate in the same
        industry as the firm. Relative to the significant different-industry spillover of
        0.17 percentage points, the same-industry spillover is larger by 0.42 percentage
        points. Column 2 shows a similar pattern for the restricted sample of
        manufacturing firms, but perhaps due to the reduction in power the difference
        between the effect of the two peer types is not significant any more. The positive
        and significant cross-industry spillovers mitigate identification concerns related
        to clustering by industry. And the larger same-industry spillovers highlight the
        societal benefit of sorting firms based on industry for increasing the overall
        adoption rate of good business practices. Finally, to measure import diffusion
        within a product category, we modify our specification in two ways. First, we
        estimate separate regressions for each product category, using a sample of
        observations in which the firm has not yet imported the given product category
        from a specific country, and including as controls indicators for whether the firm
        has imported other product categories from that country before. Second, our right-
        hand side variables are indicators for “same-product importer peers”—that is,
        peers which have imported in the past the given product category from the specific
        country—and “different-product importer peers”—that is, peers which have only
        imported in the past different product categories from the specific country. The
        last four columns of Table 11 show the results for each of four product categories
        defined based on the BEC categories. The effect of different-product importer
        peers is significant in all four categories; and same-product spillovers are
        always higher, significantly so in three of the four cases. We conclude that
        spillovers are larger within a product category, which is intuitive if part of
        importing knowledge is product-specific and further strengthens the argument about
        sorting firms based on industry to maximize spillovers.25

<h>COUNTERFACTUAL POLICY ANALYSIS</h>
------------------------------

In the presence of spillovers, policies that encourage firm trade can have additional
indirect effects through a social multiplier (Glaeser et al., 2003). And when spillover
effects are context-dependent, so is the size of the multiplier, opening the possibility
that targeted trade policies generate larger social gains. In this section we use our
estimates of the import spillover effect in a counterfactual analysis to explore how the
size and composition of a firm's peer group shape the social multiplier. Our goal is to
compute the model-implied effect on the number of importers of a non-importer firm's
exogenously induced entry into importing. To do this we assume that import spillovers
follow a simple diffusion model whose parameters are determined by our estimates. For
simplicity, in the model we only allow import spillovers between peers in the same
building. We assume that the probability that a non-importer gets “infected” is linear in
the number of importing peers.26 We allow the diffusion probability to depend on both the
sender and the receiver firm's productivity type, measured with an indicator which equals
one if the firm is in the highest productivity quartile. We also allow firms to become
importers independently of spillovers, with a baseline probability which is constant over
time and across source countries, but can depend on the firm's productivity type. We
assume that all spillover and baseline adoption realizations are independent from each
other and over time. Given these assumptions, the model generates a Markov process, and we
can track its dynamics, for each building, with four state variables: the number of
high/low productivity importer/non-importer firms in the building.27 To parametrize this
model we use specification (6) in Table 10, which estimates different spillover parameters
by firm and peer productivity category, and also reports the change in spillovers by the
number of experienced peers. We calculate baseline probabilities by firm productivity
category using the subgroup of firms which have no experienced peers in the same building.
Starting from an initial year s which we set to 2003, we then study dynamics in the
diffusion model in each building over a five-year horizon. In doing this, we assume that
firms do not move in or out of the building and do not enter or exit production. We also
investigate the benchmark case of the model with no spillovers, in which the diffusion
parameters are set to zero.

<hs>  The social multiplier</hs>
  ~~~~~~~~~~~~~~~~~~~~~

Here Mca(i), s+5 is the number of importers from country c on address a of firm i in year
s + 5 and Tsc(i) refers to the “treatment status” of firm i in year s, taking the value 1
if this firm is induced to start importing from country c. The numerator shows the
expected change in the number of importers after 5 years of firm i being treated. This
term incorporates import spillovers. The denominator is the corresponding treatment effect
in the benchmark model in which import spillovers are set at zero. Thus the multiplier
measures how much larger is the treatment effect in the presence, relative to the absence,
of import spillovers.28 Fig. 2 plots, in increasing order, the implied 5-year social
multiplier for all non-importer firms that have non-importer peers in our data in s =
2003. The figure reveals substantial heterogeneity. Interestingly, for about half a
percent of firms the multiplier is smaller than one: treating these firms results in a
smaller number of total importers in the presence of spillovers than in the absence of
spillovers. This is because spillovers have two effects: they increase the impact of
treating firm i, but they also increase spillovers from other importers in the building.
Because of this second force, the net effect of treating firm i can be reduced when
spillovers are introduced, essentially because spillovers from peers of i crowd out
spillovers from i. However this subtle crowding-out effect only overcomes the more
intuitive positive effect for a small share of observations. The median multiplier in the
figure is 1.03: inducing the median firm to import is 3% more effective in the presence
than in the absence of import spillovers. The 90th percentile of the multiplier is 1.13.
Thus inducing a firm to import which is located at this point of the multiplier
distribution is 13% more effective once import spillovers are taken into account. While
spillovers may not be very important for the typical firm, they seem quite important for a
significant share of firms, suggesting that targeting policies to such firms can generate
substantial benefits.

<hs>  Targeted trade policies</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

We next use our counterfactual to evaluate a hypothetical import-encouraging trade policy,
which demonstrates how targeting can improve policy effectiveness. For policy evaluation
the object of interest is not the multiplier, but rather the numerator of Eq. (7), which
measures the five-year treatment effect of inducing firm i to import from country c. In
our analysis we compare two policies: one in which we target firms for which this
treatment effect is large, and another with no targeting. For simplicity we consider an
import-encouragement treatment which is completely effective in teaching the firm how to
import from a particular country. Thus we assume that treating a firm results in it
starting to import from the country under consideration with certainty. Our targeted
policy is to treat the 1000 firms for whom the estimated treatment effect is largest,
while our non-targeted policy is to treat 1000 randomly chosen firms. To avoid
complications arising from treating multiple firms in the same building, we restrict both
policies to treat, for any given source country, at most one firm per building. And to
induce some amount of diffusion we only treat firms which have not yet imported from the
country and which have at least one other non-importer peer in the building. Evaluating
the targeted policy is straightforward, as it requires computing the numerator of (7) for
the selected firms. For the non-targeted policy the impact also depends on the specific
set of firms treated. To measure its average effect, we draw the 1000 random firms 1000
times, compute the treatment effect for each draw, and average over draws. The differences
between the impacts of the two policies are remarkable. The targeted policy yields after
five years 285 additional importers for a total of 1285 importers. In contrast, the non-
targeted policy yields, on average, 16 additional importers. In this example the targeted
policy is 26% more effective than the non-targeted policy (1,285/1,016 − 1 = 0.26). Since
the targeting is based entirely on observable firm characteristics such as the
productivity of the treated firm and its peers in the building, in principle it can be
implemented using public data. Overall, the result suggests that there can be large
potential gains from targeting interventions to firms which are likely to be good seeds
for diffusion.

<hs>  Internal consistency</hs>
  ~~~~~~~~~~~~~~~~~~~~

We now connect the simulation results of the diffusion model and the estimates of the
mover design in Section 3.3. Both of these designs evaluate the dynamic impact of having
an additional importer peer. Because they exploit different sources of variation and use a
different combination of reduced-form and structural approaches, their comparison provides
a useful test of internal consistency. As we have just seen, the counterfactual implies
that turning 1000 random firms in different buildings with non-importer firms into
importers would result in an expected 16 additional importers after 5 years. The point
estimate of the mover design implies (Table A5) that five years after an importer moves
into the building, the probability of an incumbent starting to import increases by 0.73
percentage points. Because the average number of incumbent firms in a building is 4.6, the
latter estimate implies that turning 1000 firms in different “non-importer” buildings into
importers would result in 0.0073 ⋅ (4.6 − 1) ⋅ 1000 = 26.28 new importers. This has the
same order of magnitude as the counterfactual, and given our standard errors we cannot
reject that the two are equal. We can also check intervening years. Table O9 in the Online
Appendix reports the expected number of firms starting to import 1–4 years after the above
treatment in both designs. Here too, the numbers have the same order of magnitude and
given the confidence intervals we cannot reject that they are equal. These patterns are
especially remarkable because the mover and the counterfactual design use somewhat
different samples: for example, in the mover design the 5-year effect is identified from
moves in the subperiod 1994–1998. We conclude that exploiting different designs and
sources of variation lead to similar estimates of the dynamics of knowledge spillovers,
providing internal consistency to our results.

<h>CONCLUSION</h>
----------

In this paper we documented evidence for import spillovers. Exploiting source-country
variation, precise spatial neighborhoods and plausibly exogenous firm moves in two
complementary research designs, we obtained credible estimates of diffusion in spatial and
managerial networks. We also documented that spillovers are stronger when firms or peers
are better, and exhibit complementarities in firm and peer productivity. Taken together,
these two results show that both high network density, and positive sorting in a given
network, can increase diffusion. We then conducted a counterfactual analysis showing that
due to the combination of these two forces the social multiplier of importing is
heterogeneous, so that targeted import subsidy policies can have substantially larger
effects. In combination, our results highlighted one concrete benefit of firm clusters:
that of facilitating the diffusion of good business practices. More broadly, our analysis
contributes to a growing literature highlighting the importance of business networks in
shaping economic outcomes.


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<ART>Living like there's no tomorrow: The psychological effects of an earthquake on savings and spending behavior
================================================================================

Authors: Mateusz Filipski, Ling Jin, Xiaobo Zhang, Kevin Chen
DOI: 10.1016/j.euroecorev.2019.04.004
Year: 2019  |  Pages: 107-128
ASJC codes: 2002, 2003
Keywords: Carpe diem, China, Disaster, Savings, Spending

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<h>ABSTRACT</h>
--------

Natural disasters impact economies not only through physical damages, but also by affecting survivors emotionally and psychologically. This can alter their economic behavior, in ways that remain poorly understood. We present a model of post-disaster savings that reveals two opposing tendencies: the need to self-insure through increased savings, and the drive to “enjoy life while it lasts” through increased spending. We use panel datasets from China's Sichuan province, and isolate psychological impacts by focusing on those who lived in quake areas but did not themselves suffer damages or injuries. Although they did not bear economic losses, they saved less, spent more on alcohol, and played majiang (a Chinese game)more often, suggesting that the “no tomorrow” tendency dominated over the precautionary tendency. The magnitude of the savings rate impact, a drop of 0.17 percentage points for each percent of distance closer to the epicenter, is economically significant, and persists in the medium term.

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<h>INTRODUCTION</h>
------------

Economists have studied how households cope with negative shocks using mitigation
strategies such as consumption smoothing (Townsend, 1994), income smoothing (Takasaki et
al., 2010), or saving (Paxson, 1992). Udry (1995) showed that households increase their
saving when they anticipate a weather shock, then tap into their savings after the shock
strikes. These studies have in common that they describe behaviors that can largely fit a
“precautionary savings” model: households build up buffers to protect themselves against
potentially negative outcomes when they anticipate a loss. Such behavior may become more
salient after experiencing a shock, such as an earthquake. However, exposure to a shock,
in particular a deadly one, may also lead people to reflect on their own mortality.
Realizing that life is fleeting leads people to discount future events, prompting them to
save less. We call this the “live like there’s no tomorrow” or “carpe diem” model.1 For
instance, after negative shocks, people are more likely to lower investment in education
(Fortson, 2011) and increase unsafe sexual behavior (Oster, 2012). This is also sometimes
referred to as a “nothing to lose” attitude (Harris et al., 2002; Hill et al., 1997).
These two channels pull an agent’s savings behavior in opposite directions. The
“precautionary savings” channel leads someone to spend less and save more, while the “no
tomorrow” channel leads to higher spending and lower savings. Different people may be more
affected by one channel or the other. Thereby the overall impact of a disaster on savings
behavior will depend on which of these two effects dominates on average. The first
contribution of this article is to provide a theoretical and analytical framework which
explains why the empirical results in the literature may go in opposite directions. We
show how the existence of two types of risk, the risk of losses and the risk of death, can
produce such antagonistic responses. The second contribution of our work is empirical. We
study how these phenomena were reflected in people’s economic behavior following the 2008
earthquake in Sichuan (China), benefiting from before–after panel data. To isolate the
psychological impacts of the quake, in most of our analysis we exclude from the sample
disaster victims who suffered damages or injuries. This is because their spending and
savings are affected by the necessities of reconstruction, so by excluding them we can
rule out the “consumption smoothing” impact channels. Instead, we are looking at
households who did not directly suffer damages nor injuries, but did witness destruction
around them, and thus would still be affected psychologically. We examine whether this
group of households start saving more (the “precautionary savings” channel), or rather
start saving less (the “live like there’s no tomorrow” or “carpe diem” channel). Our
empirical analyses suggest the latter channel dominates. The data we have access to are
uniquely appropriate for a study of disaster impacts for three reasons. First, earthquakes
are among the least predictable and most sudden type of natural disaster: while some areas
around the globe are known to be more earthquake-prone than others, the exact location of
the epicenter within those zones is as good as random. This makes earthquakes uniquely
suitable for use as a natural experiment. Second, the intensity of earthquake damage can
be precisely measured. For most types of disasters, intensity can be hard to gauge, and is
often approximated by the extent of damages. But using damages as an intensity variable
poses problems of endogeneity, because areas more damaged are not necessarily those where
nature struck hardest. The extent of damages may be more related to preparedness (an
endogenous variable) than to the intensity of the natural shock (an exogenous variable).
Those who tend to save less for the future may also be those who incur the most damages in
a disaster, so the cause-consequence relationship between damages and savings behavior is
blurred.2 Modern seismology provides measurements that can pinpoint the origin and
magnitude of tremors with great precision. The distance to the epicenter is a fully
exogenous proxy for intensity and is also remarkably easy to compute.3 Third, we have
access to both pre-earthquake and post-earthquake data. Using three separate sources, we
were able to compile a unique panel dataset spanning a vast area around the epicenter of
the earthquake over three years: 2007 (pre-earthquake), 2009 (one year post-earthquake),
and 2011 (three years post-earthquake) for our analysis. In addition to household savings,
we also look at other behaviors: the time people spent playing majiang (a Chinese 4-player
game sometimes called mah-jong), as well as their expenditures on alcohol, as supporting
evidence. Our study contributes to the literature on natural disasters. Economic studies
of natural disasters tend to focus either on physical damages, such as the costs of losses
and reconstruction (Anderson, 1990; Mechler, 2004; Toya and Skidmore, 2007), or on
macroeconomic consequences, such as the impacts on growth (Cavallo and Noy, 2009;
Hallegatte and Przyluski, 2010; Noy, 2009). The psychological literature, on the other
hand, places greater weight on emotional damages, such as the prevalence and persistence
of depression or post-traumatic stress disorder (PTSD) (Madakasira and O’Brien, 1987; Yule
et al., 2000). At the nexus of these literatures lies the fact that disasters influence
economic systems through changes in the psychology and behavior of economic agents. Yet
while this phenomenon is sometimes alluded to in both literatures, it is seldom explicitly
treated. Our paper fills this lacuna. Our work also relates to the literature on the
impacts of exposure to shocks on risk preferences. That literature tends to focus on risk
aversion as elicited through experimental designs (choice lotteries etc.) rather than on
economic variables (savings) as we do in this paper. However, our focus on the
psychological nature of these impacts makes the connection relevant. As shown in Chuang
and Schechter’s (2015) compelling review, the findings of this literature are mixed: while
some find that agents became more risk-averse after a disaster (Cameron and Shah, 2015;
Cassar et al., 2011; Chantarat et al., 2015), others find the opposite (Bchir and
Willinger, 2013; Cameron and Shah, 2013; Eckel et al., 2009). Another comprehensive review
suggests that measures of risk preferences are unstable over time (Schildberg-Hörisch,
2018). While our paper does not treat of risk aversion directly, the theoretical framework
we develop provides a lens that accommodates such conflicting findings. One paper standing
out in that literature is Hanaoka et al. (2018): it shows that males who experienced a
higher intensity of the Great East Japan Earthquake exhibit decreased risk aversion, and
also increased risky behaviors such as drinking and gambling. Their finding is consistent
with a dominance of what we call the “no tomorrow” channel. However, they do not examine
the impact on savings behavior, which is a focus of our paper and a key economic variable.
The next section illustrates the “precautionary savings” and “no tomorrow” savings
behaviors in a theoretical model, reviews the literature, and outlines our empirical
strategy. Section 3 describes the background and data. Section 4 presents results as well
as discussions on the robustness and the economic significance of those results.
Conclusions follow.

<hs>  A simple model of disasters and savings behavior</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We develop an analytical model to illustrate the conflicting tendencies towards saving and
dissaving that result from the psychological effects of an earthquake, emerging from the
opposing “precautionary savings” and “no-tomorrow” tendencies. The model is rooted in the
expected utility framework, in the spirit of Sandmo (1970) and several prominent
publications that followed (Carroll, 1997; Deaton, 1991; Hubbard et al., 1994, 1995).
Where δ is a discount factor, U a standard “well-behaved” utility function (increasing,
twice differentiable, concave), and Ct is consumption at time t and depends on the
probability of losses. The horizon is theoretically infinite, but in practice an agent
will eventually die, after which their consumption is reduced to zero (the second term in
the brackets). These inequalities show that the optimal amount of savings increases with
the risk of suffering losses. This is the “precautionary savings” effect. On the other
hand, the optimal amount of savings decreases with the risk of death, the “no tomorrow”
effect. The two effects work in opposite directions. Fig. 1 provides graphical
illustration of the “precautionary savings” and “no tomorrow” effects under specific
values for ρL, and ρD.4 When both ρL and ρD are zero (case a: no earthquake) the agent
simply splits total wealth in half, to consume equal amounts in the two periods. When ρL =
1 (case b: losses, but not death, are anticipated with certainty and equal to L), the
agent saves an additional L/2 in the form of “precautionary savings”. When only ρD > 0
(case c: death is possible) the agent will consume more in period 0, up until the limit
case ρD = 1 (death is certain), when the agent has no reason to save for the next period
and consumes everything immediately (the “no tomorrow” effect). All intermediate cases
with ρD > 0 and ρL > 0 will combine the two tendencies, and the balance between the two
will determine whether the agent will save more, or less, than a no-risk equal split. We
can use this conceptual framework to guide our analysis of the savings behavior of agents
in Sichuan after the earthquake. Although the true values of ρL and ρD may not be affected
by the earthquake, it is how agents perceive those probabilities that matters. That
perception may change after experiencing an earthquake. Witnessing the quake adds
information about the possibility of such an event (and the possibility of aftershocks),
leading the agent to increase the perceived values of ρL and ρD.5 This would be true for
all agents who did not know an earthquake could occur, or who underestimated how
destructive or deadly an earthquake could be. Furthermore, even if agents had perfect
information and knew the true probabilities of earthquakes prior to the event, behavioral
economics and prospect theory suggest that agents act irrationally by placing excessive
weight on more recent events, due to “salience” or “availability bias” (Tversky and
Kahneman, 1973). People are more aware of disaster risk after a disaster, regardless of
what the probability truly is (Asgary and Levy, 2009). Finally, ρL and ρD are not limited
to the probability of earthquake damages/death, but all types of adverse events.
Experiencing the earthquake leads to better information and greater salience of the
unpredictable and fleeting nature of life in general, which also increases perceived ρL
and ρD. Thus, only agents that are both perfectly rational and perfectly informed would
not increase their perceived probabilities of ρL and ρD.6 Excluding economic impacts of
the quake, the psychological impacts would lead an agent to react in one of three ways: If
the agent is entirely rational and perfectly informed, they will not change their
perceived probabilities ρL and ρD, and should not alter their savings rate. If the agent
increases perceived probabilities and the effect of ρL dominates, they should engage in
“precautionary savings” and increase their savings rate. If the agent increases their
perceived probabilities and the effect of ρD dominates, they should adopt a “no tomorrow”
attitude and decrease their savings rate. Which effect will dominate is influenced not
only by the values ρL and ρD, but also by the size of the potential losses and other
idiosyncrasies of the agent’s situation. The rest of the paper is dedicated to showing
empirically that, in the case of our data, the “no tomorrow” effect was dominant.

<hs>  Empirical framework and identification strategy</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Three considerations are worth mentioning. First, we exclude the households which suffered
direct damage in our main analysis. The destruction caused by the earthquake requires
reconstruction expenditures that will force households to save less through sheer economic
necessity – that is not the impact channel we are concerned about. The goal of this paper
is to document the shifts in savings and other behaviors that are driven by psychological
and emotional channels. We solve this problem by restricting our sample to those
households whose homes did not suffer damages and who did not suffer injuries nor death.
Such households do not incur reconstruction expenditures, but likely observed destruction
around them, which could still trigger responses through the “precautionary savings” and
“no tomorrow” impact channels, as they update the perceived probabilities of losses or
death occurring. The same goes for health-related expenditures, funeral expenditures, etc.
Another way to deal with this problem is to change the left-hand-side variable from the
savings rate to something less affected by reconstruction costs. We estimate impacts on
the frequency of playing majiang and on alcohol expenditures, which are less obviously
related to the need to rebuild or reinforce a house. Secondly, our identification strategy
helps isolate the psychological impacts, but it also comes with some drawbacks. One
concern is the possibility that selecting the sample in that way introduces selection
bias. We dedicate a part of the results section to ruling out these effects by running
various tests and working with the full sample. Thirdly, in regard to our choice of
distance-to-epicenter as a measure of earthquake intensity. At first glance, an obvious
choice for an intensity variable would be the damage to someone’s house – but this raises
the “Three Little Pigs” endogeneity issue discussed in the introduction. Destruction at
the village level poses less of an endogeneity problem (though it does not fully solve it,
because people with similar behaviors may tend to live in the same villages). An agent’s
beliefs and attitudes are also influenced by the intensity of damage to the village in
general (for instance, if a neighbor’s house was destroyed or the local school collapsed),
so village-level damages are a better intensity measure for our purposes. We use village-
level damages, deaths, and injuries as robustness checks and for certain specifications.
Distance to epicenter, however, is arguably most likely to be exogenous, which is why we
make it our preferred intensity measure.7

<hs>  The Wenchuan earthquake</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

The province of Sichuan is located in southwestern China. At the point of contact between
the Tibetan plateau and the eastern fertile basins, the region’s topography is highly
uneven. Tectonic tensions between the Indian and Eurasian plates created the Longmenshan
Fault, responsible for the seismic activity that resulted in the 2008 disaster. The 2008
earthquake took place on May 12, with its epicenter in the county of Wenchuan. The
location of the epicenter is shown in Fig. 2. The original seism reached a magnitude of 8
on the Richter scale. It was followed by strong aftershocks spreading toward the northeast
along the fault line, many of which were also of considerable magnitude (also on Fig. 2).
The damage of the earthquake spread through the entire region and even affected Gansu, the
province to the north. The Sichuan earthquake of 2008 was among the most destructive
earthquakes in recorded history: it killed at least 69,000 people, and left between 4.8
and 11 million people homeless (Bulte et al., 2018). The extent of the damage captured
national and worldwide attention. The collapse of school buildings and the number of child
casualties exacerbated the emotional shock, fueled anger against officials involved in
school construction, and triggered a corruption scandal. The severity of the disaster
prompted the Chinese government to launch a swift reconstruction effort of unprecedented
scale. Reconstruction was fully complete in less than four years (Yang, 2012). The full
economic impacts of the earthquake, however, may have been longer lasting, including
through the psychological channels we set out to document.

<hs>  Data sources and summary statistics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Data sources. Because natural disasters are difficult to predict, it is rare for
economists to have the pre-disaster data necessary for solid econometric estimations. Our
work was made possible by constructing a unique dataset which merges three household
surveys: the Sichuan component of the annual rural panel collected by the Chinese Ministry
of Agriculture’s Research Center for the Rural Economy (RCRE), a supplementary survey
administrated jointly by the RCRE and the International Center for Agricultural and Rural
Development (ICARD), and the Sichuan Rural Household and Migration Survey (SRHMS)
administrated jointly by the Shanghai University of Finance and Economics and ICARD. The
design of the RCRE and SRHMS surveys has enough in common that merging them presents only
minor compatibility concerns. The RCRE dataset is a national rural panel collected
annually since 1984, and one of the most widely used data sources on rural China. It
includes about 800 household observations in the Sichuan province, collected from 16
villages. While all of those villages experienced some level of earthquake (it was felt as
far as Beijing), 5 of them were designated as directly affected by the earthquake
according to government classification, and 1 as severely affected. This may limit
explanatory power for earthquake-related questions. The SRHMS was started in 2007 and
gathered information on about 800 households from 6 villages. The SRHMS focused
specifically on Mianzhu County, which was later to become one of the most severely
affected counties in the 2008 earthquake. The SRHMS was repeated after the earthquake, in
2009 and 2012. By merging 2007, 2009, and 2011 data from the RCRE, the supplementary RCRE
data, and the SRHMS, we obtain a unique panel dataset that spans all of Sichuan, has a
considerable number of observations in severely affected areas, and includes a pre-
earthquake baseline.8 A full description of the datasets exists in Jin et al. (2013), and
the location of villages is shown in Fig. 2. Our full sample contains 22 villages and 1306
households.9 The restricted sample of households whose homes were not damaged, suffered no
physical injuries nor deaths as a result of the earthquake, is 589 for each year (1767
observations in total). We used Global Positioning System (GPS) coordinates to compute
distances between villages and the epicenter of the earthquake (shown in Fig. 2).
Coordinates for villages were obtained from the online mapping website map.baidu.com. All
epicenter coordinates came from the United States Geological Survey (USGS).10 We also used
mapping software to match each village with seismic intensity estimates publicly available
from the USGS website.11 We culled consumer price index (CPI) values from the Sichuan
Statistical Yearbook (SBSP, 2007, 2009, 2011) using the CPI in the nearest county where
data are available. Explained variables. Household surveys seldom collect data on cash
amounts saved by households, such that savings need to be computed as the difference
between yearly income (Y) and yearly consumption expenditures (C). A common practice
introduced by Deaton (1977) is to approximate the savings rate as r = ln(Y) – ln (C) =
ln(Y/C), the natural log of the income-consumption ratio. This measure has the advantage
of limiting the power of outliers (Chamon and Prasad, 2010; Deaton and Paxson, 1994, 2000;
Wei and Zhang, 2011), and we use ln(Y/C) as our main measure of the savings rate.12 In the
appendix we also show that results are similar when using s = (Y – C)/Y as the dependent
variable, but this measure is less preferred due to outliers (see violin plot in Appendix
Fig. A1). Other explained variables we use include expenditures on alcohol (expressed in
Chinese renminbi, or RMB), and majiang frequency (expressed as the summed number of times
per month any member of the household played majiang). All variables used in the analysis
are presented in Table 1. The mean savings rate ln(Y/C) approximation in the sample is
0.62, the mean expenditure on alcohol is 63 RMB per month, and the mean frequency of
majiang 3.1 times/month.13 For the dependent variables we also compare means in different
years in Table 2: only alcohol expenditures dropped enough in 2009 to show significance in
the t-tests. Earthquake variables. Our measure for earthquake intensity is the distance
between a village and the epicenter of the seism. It was computed from GPS coordinates
using geographic information systems (GIS) software in the World Geodetic System (WGS)
1984 Universal Transverse Mercator (UTM) Zone 48 N coordinate system. The average distance
to epicenter was 236 km (sd = 95 km). We also use the village-level shares of deaths and
injuries within the sample resulting from the earthquake, and the share of collapsed
houses, as measures of how deadly/destructive the earthquake was locally. Control
variables. The bottom of Table 1 provides statistics for the control variables used in the
analysis, for the sample of non-affected households. All our specifications control for
head gender, age, age squared, party membership, and education; household size, size
squared, and landownership. In addition, the key observables we control for are household
incomes, job loss in the household, consumer price index, amounts gifted, loaned, and
received as government transfers. Appendix Table A1 shows how those variables vary by
year. Incomes grew somewhat over the period, as did prices. There was an expected increase
in government transfers received (significantly higher than the base year for both 2009
and 2011). Gifts to other households increased significantly, but only in 2011. The
average age of the household head increased (also expected for a panel), and landholdings
are slightly smaller in 2011 than in 2007. Most other differences in the table, such as
the slight decrease in number of laborers per household, are of moderate magnitude and
insignificant according to means-equality tests.

<hs>  Impacts on the saving rate</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~

The central result of our analysis is that households who were not directly affected by
the earthquake reduced their savings rate, even after controlling for confounding factors.
This result suggests that (1) the change in saving and spending behavior after the
earthquake is at least in part due to psychological motivations; and (2) that the “no
tomorrow” effect dominates the “precautionary savings” effect. We first illustrate this
result graphically. We chart out the average change in the savings rate in the two years
after the earthquake, by distance to epicenter, in Fig. 3. A negative value means the
savings rate decreased in 2009 compared to 2007. The observations display a clear rising
pattern, with a drop in savings rate in areas closer to the epicenter. The figure displays
only “unaffected” households, whose houses were not destroyed, who reported no
reinforcement expenditures, and whose members suffered neither injuries nor bodily harm.
The figure shows that unaffected households closer to the epicenter tended to reduce their
savings rate. Since unaffected households face no direct economic shocks to alter their
savings behavior, the change in savings rate we observe closer to the epicenter may
instead be driven by psychology (the “no tomorrow” effect). However, before we can claim
to have estimated this psychological effect, we first need to rule out all other
confounding factors and competing explanations in multivariate regression analysis. Table
3 shows the impacts of proximity to epicenter on the savings rate of households, using the
framework specified in Eq. (10).14 Samples are restricted to unaffected households. All
columns present the results of ordinary least squares (OLS) regressions with household
fixed effects, thus differencing away any potential effect of time-invariant household
characteristics. Each specification is run with the ln(Y/C) approximation of the savings
rate as the explained variable.15 All specifications contain controls for household
characteristics that may vary over time: household head’s gender, age, age squared, party
membership, and education, as well as household size, size squared, landholdings – those
coefficients are not presented in the table in the interest of space, and excluding them
from the regression does not alter results.16 The explanatory variables of interest are
the interaction terms between the distance to epicenter and the year dummies. They measure
the effect of earthquake on change in savings rate relative to the base year, 2007. The
intensity*2009 interaction term can be thought of as a short-term impact. The 2011
interaction term reveals medium-term impacts, at a time when much of the reconstruction
effort was complete. Column (1) of Table 3 shows that the coefficient for the 2009
interaction terms is positive and significant (0.156). After the quake, households closer
to the epicenter reduce their savings rate. How can we explain this earthquake-induced
drop in savings rate for households who suffered no losses? We know that the significant
coefficients in column (1) cannot be due to expenditures on reconstruction/repair of their
home or other belongings, nor health or funeral expenditures. It cannot be due to the loss
of children or dependents either (households who lost a dependent could anticipate a
reduced need for savings), as households in the sample did not suffer human harm either.
We also control for household size, so we can also rule out explanations based on
dependents leaving the home. However, there are other alternative impact pathways that
could explain this result. We identify four such plausible hypotheses, and attempt to rule
them out in columns (2) through (5) in Table 3. The first alternative explanation is the
“income hypothesis”. The literature generally agrees that there exists a relationship
between incomes and savings rates, i.e. richer households tend to save more as a
proportion of their income (Lawrance, 1991). Facing a negative income shock, households
may choose to lower their savings rate in order to maintain consumption. Similarly, if the
household lost certain sources of income or employment it could alter its savings rate. We
test this “income hypothesis” in columns (2) (and the following columns) by including
household incomes as a control variable, as well as a control for whether the household
lost a worker since the last survey round. This hypothesis is borne out with a strongly
significant coefficient (0.172) on the income variable: households whose incomes rose more
also saved more as a proportion of that income. Further, once we account for incomes, the
2011 distance coefficient also becomes significant (0.227), suggesting that the impact of
the earthquake persisted into the medium run. The R-squared measure also increases
dramatically once we add incomes, confirming that this hypothesis holds explanatory power
– but not enough to explain away the savings rate effect (Table A2). In addition, we show
in appendices Fig. A2 and Table A4 that the savings rate impact we measure for unaffected
households is driven by expenditures, not incomes. Fig. A2 shows graphically that distance
to epicenter appears unrelated to the pre-post difference in household income.
Expenditures, on the contrary, rose more in households closer to the epicenter, as
demonstrated by a downward sloping trendline with highly significant coefficients. Table
A4 confirms these results in a regression framework, and shows they are robust to all
control inclusions. This further suggests that the savings rate effect we document is
driven by the expenditure side, rather than by any income effects. The next possible
explanatory factor is price inflation, which reduces incomes in real terms (or,
symmetrically, increases the cost of consumption). Under this “inflation hypothesis,”
households closer to the epicenter would be saving relatively less because their
purchasing power for tradeable goods decreased. We test this by adding a measure of local
consumer price index as a control variable, starting in column (3), but find it barely
alters the other coefficients. Another possible explanation may be that unaffected
households helped their affected friends or relations: the “altruism hypothesis”. Yet
another possibility is that households in more affected areas received a greater amount of
government assistance, even if their homes were not destroyed (some programs are location
based). Households may tend to treat transfer income differently from earned income (the
“nonfungibility hypothesis”), which could explain their lower savings rate. We try to rule
out these two options by including measures of gifts and loans extended by households in
column (4), and government transfers they receive in column (5). None of this influences
results. Finally, the drop in saving rates could be due to a change in psychology, the
“live like there is no tomorrow” or “carpe diem” hypothesis. Unfortunately, we do not have
access to any variable that would allow us to directly measure this. However, since our
results suggest we can rule out the income, inflation, altruism, and nonfungibility
hypotheses, this would suggest that the “no tomorrow” hypothesis might be at play. It
seems to affect the savings rate significantly, and to persists in the medium term. An
additional concern regarding our results may arise from the fact that the number of
villages in our data is small. All our regressions use cluster-robust standard errors,
which is superior to uncorrected standard errors, but nevertheless imperfect.
Specifically, it has been shown that one might over-reject null hypotheses when the number
of clusters is small (Cameron et al., 2008, 2011). Therefore, we also performed wild
bootstrapping tests on the two interaction terms coefficients as a post-estimation
procedure (Cameron et al., 2008; Canay et al., 2018). The p-values derived from this
procedure are included at the bottom of the table, and confirm our result: all of the 2009
and 2011 coefficients are strongly significant. The size of the impacts we measure is
economically significant. They can be interpreted as follows: being one-percent closer to
the epicenter is associated with a 0.17 percentage point decrease in the savings rate on
average in 2009, and a 0.22 percentage point decrease in 2011. This translates to a
distance-to-savings elasticity of about 0.3. In terms of the common earthquake intensity
measure used in the media, the savings rate drops 20 percentage points for each degree on
the Richter scale.17 Not only is this effect economically meaningful, it persists in the
medium term, with a slight increase.

<hs>  Physical destruction versus human harm</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We further test the insights from our analytical model by focusing on the extent of death
and destruction at the village level. If the model is correct, households in areas which
experienced more death should exhibit more pronounced “no-tomorrow” behavior. Areas that
experienced destruction, on the other hand, would likely exhibit more tendency for
precautionary savings. Naturally, both effects will be at play in both types of villages,
since death and destruction are correlated. In addition, with the existence of media, all
households are likely aware of the extent of losses and casualties in the region.
Nevertheless, we can expect households in villages where no deaths occurred to exhibit a
muted “no tomorrow” response compared to those who witnessed deaths first-hand. We run OLS
fixed-effects regressions on the savings rate measure using rates of death, injuries, and
damages as measures of earthquake intensity in Table 4. All specifications include all the
previously identified relevant controls. Column (1) shows that the share of deaths at the
village level is significantly related to lower savings rates in 2011 (−0.177), though it
is not significant in 2009. In columns (2) we see that the same is true of the share of
injuries, though the magnitude of coefficients is much smaller (−0.03). In column (3), we
see that a higher share of collapsed houses also leads to a lower savings rate, this time
with significance both in 2009 and 2011, but again a smaller magnitude compared to the
death rate. Finally, we re-ran the specification with collapsed houses, but limiting only
to villages where no death occurred. This unfortunately leaves us with a rather small
sample and we should not overinterpret the result, but nevertheless we find a positive and
significant relationship in both 2009 and 2011. These findings bolster the hypothesis that
witnessing death exacerbates the “no-tomorrow” channel, while witnessing damage favors
“precautionary savings”. In the next section we move beyond the savings rate, and estimate
impact on other outcome variables. We look at alcohol expenditures, and the frequency of
playing majiang, both of which reflect “no tomorrow” attitudes. In addition, since these
behaviors are not straightforwardly related to house rebuilding, the results also serve as
a further robustness check supporting the notion that the change in behavior we observe is
not driven by earthquake damages but rather by psychology.

<hs>  Impacts on alcohol expenditures</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Agents with a “living like there is no tomorrow” attitude can be more likely to engage in
behaviors that bring about immediate reward but may cause delayed harm, because they
expect they might die before those bad outcomes occur. One such behavior is the
consumption of alcohol, which is known to be detrimental to health, but with symptoms that
tend to develop over the long run.18 Under our “no tomorrow” hypothesis, we can expect
agents closer to the epicenter to increase their alcohol intake relatively more. Table 5
presents the results of regressing the logged monthly alcohol expenditures on distance to
epicenter (column (1)) using OLS and household fixed effects, with all the basic controls
(age, education, etc.). We then include all the additional controls that help rule out the
alternative explanations to the “no tomorrow” hypothesis in column (2). Column (1) shows
negative and significant signs on the distance interaction terms for 2009 and 2011:
households closer to the quake epicenter increased their alcohol expenditures more than
those further away from it. Results persist in column (2), ruling out alternative
explanations. Given the large number of nondrinkers in the sample, a Tobit specification
left-censored at zero may be more appropriate to capture the alcohol expenditure
decisions.19 We present those results in columns (3) and (4), mirroring the specifications
of the first two columns. We find negative and significant coefficients in both years and
both models. This result echoes that of Hanaoka et al. (2018), who found that Japanese men
increased their drinking behavior after an earthquake. The OLS coefficients of interest,
ranging from −19.95 to −25.61, can be interpreted as follows: being one percent closer to
the epicenter increases the monthly expenditure on alcohol by about 0.2 RMB. This is about
0.3% of average expenditures, which is far from negligible. It is noteworthy that,
similarly to the savings rate results, the effect on alcohol expenditures seems to
intensify in the medium term (2011), with all 2011 coefficients being larger and more
strongly significant than the 2009 coefficients. This may be due to the addictive nature
of alcohol consumption. Addictions formed or reinforced in the aftermath of the earthquake
may be harder to shed than other behaviors.

<hs>  Impacts on playing majiang</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~

The game of majiang (or mah-jong) is a popular pastime throughout Sichuan, as in much of
eastern Asia. While the game often involves some financial stakes, those are usually small
enough to be considered symbolic, such that playing majiang is primarily a form of
entertainment rather than gambling. Either way, agents displaying a “no tomorrow” attitude
would be expected to engage in it more often, either because they are more willing to
gamble with their money, or simply because playing games with friends is a way to “enjoy
life while it lasts”.20 The 2007 and 2011 surveys asked how frequently household members
played majiang, in number of times per month. This part of the questionnaire was not
administered in 2009, which limits us to estimating only the medium-term effects, three
years after the earthquake. Table 6 presents the results of regressions of majiang
frequency on the distance from epicenter. Majiang frequency is expressed as the average
number of times someone in the household played majiang in a month. Because the frequency
can be thought of as a count variable, so we also ran the regression as a Poisson model
with fixed effects (columns 3 and 4). We can also think of it as a continuous variable
truncated at zero, so the fifth and sixth columns use a Tobit model left-censored at zero
with random effects. We obtain negative and significant coefficients across the board.
Households further away from the epicenter increased majiang frequency less than those
closer to it. This is robust to the inclusion of additional controls for income levels,
prices, altruism and transfers, thus bolstering the “no tomorrow” hypothesis. Again, it is
noteworthy that we find a strongly significant impact in 2011, suggesting that this
behavior change existed in the medium term.

<hs>  Ruling out selection bias</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~

Most results in this paper are based on the model in Eq. (10), which minimizes endogeneity
issues by restricting the sample to unaffected households, ridding us of the effect of
reconstruction expenditures. However, this model is not immune to criticism. The chief
concern is that by restricting the sample to unaffected households, we may be introducing
some selection bias. In this section we show that this is unlikely the case. The important
question is whether the selection criterion (being an unaffected household) picks
households differently across areas. In other words, are households selected into the
sample more unusual when they are close to the epicenter than when they are far away? To
test whether that is the case, we computed, for all variables used in the analysis, the
z-score for each household within their village (z = (x − µ)/σ, where x is a household
observation and µ and σ are the mean and standard deviation of that variable in a given
year). We then regressed, for selected households only, each of these z-score variables on
the distance from epicenter, the year of the survey, and the distance*year interaction
terms. Table 7 shows results for the three explained variables we use in the paper and the
four main control variables. Table A6 in the appendix shows results for all the other
variables. None of the regressions show any significance on the distance*2007 coefficient
(bolded). This suggests that, prior to the earthquake, the households that ended up
selected into the sample were no more unusual close to the epicenter than those further
away. In fact, there is also no significance for the distance*2009 coefficient, suggesting
that even after the earthquake the close-by households were still not more unusual than
those further away. The second way we can verify that selection bias does not drive our
results is by running specifications using the full sample. Table A5 repeats the same
specifications as Table 3, but does not use the selected sample. Using the full sample, we
obtain nearly the same results as using the selected sample, suggesting selection is not
the driver here. In Table 8, we use the specification in Eq. (11), controlling for all the
previously discussed covariates, and also adding controls for the amount borrowed for
house reconstruction, which could influence expenditure patterns. Unfortunately, for lack
of data we are not able to control for whether the loan is still being repaid or not.
However, Jin and Chen (2014) find that less than a third of rebuilding and reinforcement
costs were financed with loans, minimizing the extent of this issue. Results in all three
columns confirm almost all results presented above: both 2009 and 2011 coefficients are
significant for the savings rate, alcohol expenditures rose significantly in 2009
(insignificantly in 2011), and majiang frequency also increased in 2011, consistently with
our “no tomorrow” hypothesis.

<hs>  Ruling out price transmission</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Prices influence consumer behavior, which is why our regressions control for price levels
by including the CPI as an explanatory variable. However, we may still worry that CPI is
too coarse a measure of local price fluctuations. Unfortunately, we do not have local
panel data that would allow us to include specific price levels (say, of alcohol) in the
regressions we present. What we can do is to test whether, in general, rural markets
throughout Sichuan are well integrated. If they are, then we should be reassured that
geographic differences in price fluctuations are likely not what explains the changes in
consumer behavior that we document.

<h>CONCLUSIONS</h>
-----------

Even when their home was not affected by the tremors, households who live closer to the
2008 earthquake reduced their savings rate, increased their purchases of alcohol, and
played majiang more often after the disaster. Our estimates are significant in 2009, and
most persist into 2011. Results are not explained by incomes, prices, altruism, or non-
fungibility of income sources, suggesting that these changes may be reflecting the
psychological impacts of the earthquake. The results are broadly consistent with a model
under which agents lean towards a “no tomorrow” attitude, rather than towards
“precautionary savings.” Those who lived in villages with higher death rates also reduced
their savings, but the same is not true for rates of physical damage, further supporting
the notion that the “no tomorrow” channel may be at play. We can only conjecture what the
precise mental and emotional pathways might be that underpin our results. Some agents
might be making the rational calculation that they may not live long enough to make use of
their savings. Others might prefer not to accumulate assets that can be destroyed
unexpectedly. Agents may be focusing on present enjoyment, or, conversely, be suffering
from depression. A number of villagers may be affected by PTSD, which has also been
associated with increased spending.24 The exact mental pathways that led to our results
may differ between agents in the sample, and further generalization requires more
research. While we cannot verify which mechanism is most prevalent in our data, all are
broadly consistent with the “no tomorrow” model. The impacts we document are economically
significant: the savings rate drops by about 0.17 percentage points with each percent
closer to the epicenter, or about 20 percentage points for each degree on the Richter
scale of earthquake magnitude. A population that starts saving less, consuming more,
taking on risks, and generally tending toward “living like there is no tomorrow” is likely
to substantially alter its economic path. In the medium run, we see that households closer
to the epicenter save less, spend more on alcohol, and play more majiang even 3 years
after the earthquake. Through these changes in attitudes, the consequences of natural
disasters may continue shaping life and economic growth in affected areas long after
reconstruction has been completed.25 Our analysis helps reconcile some mixed findings in
the literature. Viewed as a tug-of-war between “precautionary savings” and “no-tomorrow”
tendencies, it becomes clear why some studies find positive, others negative impacts of
disasters on risk preferences and risky behavior. It is possible that the prevalence, or
salience, of either destruction or death during a disaster can explain these conflicting
findings, as suggested by our Table 4. The Sichuan earthquake cost more than 80,000 lives.
The vivid TV images of deaths may have a much stronger psychological effect than less
deadly disasters. The study of the differential effects of deadly and non-deadly disasters
features highly on the future research agenda. Our work also brings to light another
conundrum. Economists have documented higher saving rates in more disaster-prone areas
(Skidmore, 2001). Yet we find persistently lower savings rates after the quake. This could
reflect the fact that not all disasters produce the same rates of damages and human
casualties. It could also mean that while the “no tomorrow” channel may start dominating,
it may gradually recede in the long run, and let “precautionary savings” take over. This
would be consistent with insights from behavioral economics: as time passes, the memory of
the earthquake becomes less “salient”, which may alter the balance between the two
channels. Assessing the longevity of these impacts thus provides a compelling avenue for
future research. Some of our results seem to strengthen in the medium run. This can be
highly relevant when viewed through the lens of addiction, habit formation or path
dependency. Additional research is needed to fully understand the short-, medium-, and
long-term impacts of living under the threat of disaster.


<h>REFERENCES</h>
----------

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<ART>Longitudinal determinants of end-of-life wealth inequality
==========================================================

Authors: James Poterba, Steven Venti, David A. Wise
DOI: 10.1016/j.jpubeco.2018.04.008
Year: 2018  |  Pages: 78-88
ASJC codes: 2002, 2003
Keywords: Health and wealth, Lifecycle saving, Precautionary saving, Retirement wealth, Social Security

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Inequality in wealth among elderly households, and in particular the prevalence of very low wealth holdings, can be an important consideration in the design of social insurance programs. This paper examines the incidence and determinants of low levels of financial and total wealth using repeated cross-sections of the Health and Retirement Study (HRS) and a small longitudinal sample of HRS respondents observed both at age 65 and shortly before death. Most of those who report very low wealth holdings at the end of their life had little wealth at the traditional retirement age of 65. There is strong persistence over time in reports of very low wealth, and more generally relatively little evidence that wealth is drawn down in the first 15 years of retirement. The age-specific probability of reporting low wealth increases slowly after age 65. Low lifetime earnings are strongly predictive of low wealth at retirement and at the end of life. The post-retirement onset of a major medical condition, and, for married women, the loss of their spouse, are both associated with small increases in the probability of reporting very low wealth, but they account for a small fraction of low-wealth outcomes. Low levels of wealth accumulation before age 65, rather than gaps in the safety net after 65 or rapid spend-down of accumulated assets, appear to be the primary determinant of low levels of wealth just before death.

--------------------------------------------------------------------------------


<h>THE DISTRIBUTION OF END OF LIFE WEALTH</h>
--------------------------------------

Alvaredo et al. (2016) review the primary sources of information on wealth holdings for
all the but very richest households. These are administrative (tax) data on estates at
death, which can be used to estimate the wealth of the living by applying (the inverse of)
mortality multipliers differentiated by age, sex and wealth class; administrative data
such as tax data on investment income, which can be “grossed up” to estimate the
associated wealth distribution; and household surveys, like the HRS. Tax evasion and
avoidance can make the first two sources problematic, while low response rates and under-
reporting of wealth at the top of the distribution can make surveys unrepresentative. The
HRS response rate, between 81 and 91%, is unusually high for a household survey. As with
most large cross-section surveys, the assets of the very wealthy tend to be
underreported.3 This is not a major concern for the analysis of low wealth holdings among
the poorest elderly. The HRS data have many strengths but they also suffer from several
limitations. First, the HRS samples each respondent at two-year intervals. With respect to
end-of-life wealth measures, if a respondent dies just after completing an interview, the
last recorded wealth value is a timely estimate of wealth in the last weeks of life. For
those who die many months after their last survey, however, wealth balances “at the end of
life” are measured with error. Because expenditures associated with declining health are
often substantial in the last few months of life, the reported balances in the last
interview before death are likely to over-estimate wealth at the time of death.4 Second,
there are data outliers. Some may be accurate, but others may be the result of
misreporting. To minimize their impact, we exclude records for 153 persons reporting more
than $10,000,000 or less than −$1,000,000 of total wealth. We also focus much of our
analysis on the probability that respondents report wealth below a threshold value.
Measurement errors that do not move respondents across this threshold will not affect our
findings. The HRS is a longitudinal survey that currently includes five cohorts defined by
the year in which respondents are first surveyed. The original HRS cohort surveyed
respondents between the ages of 51 and 61 in 1992 and the Asset and Health Dynamics of the
Older Old (AHEAD) cohort surveyed respondents aged 70 and older in 1993. Subsequent
cohorts include the War Babies (WB) cohort, first surveyed in 1998 when respondents were
between the ages of 51 and 56, the Children of Depression (CODA) cohort first surveyed in
1998 when respondents were between the ages of 68 and 74, and the Early Baby Boomers (EBB)
cohort that includes respondents aged 51 to 56 in 2004. All cohorts were surveyed every
second year through 2012.5 Our primary sample includes HRS respondents from all cohorts
who are known to have died and who were at least 65 years old in the last survey wave
prior to their death. Of the 33,316 individuals who were alive in the HRS at some point
between 1996 and 2012, 9215 died during this sample period. Of them, 7848 were age 65 or
older at death. For some purposes, we also analyze a much smaller set of 1073 married
respondents who were observed at age 65, the date we consider traditional retirement, and
who also died during our 16-year sample period. We refer to this as our “longitudinal
sample” because it allows us to track the full evolution of wealth and financial assets
from age 65 to death. We define wealth as the sum of home equity, the net value of other
real estate, business assets, and net financial assets. We convert asset balances to $2012
using the CPI-U, and measure them net of outstanding liabilities; both wealth and net
financial assets can be negative. Financial assets include IRA and Keogh balances, as well
as 401(k) and other defined contribution balances associated with the respondent’s current
job.6 Balances in accounts sponsored by previous employers are not included.7 Our unit of
observation is the individual, but for those who are married, we associate household
wealth with each member of the couple. It can be difficult to assign ownership of assets,
such as housing or jointly held financial assets, to specific household members. For some
tabulations, we stratify results by the distribution of household lifetime earnings at age
65. The sub-sample used to produce these results includes the roughly two-thirds of HRS
respondents who approved linking their survey responses to earnings and benefit histories
from the Social Security Administration.8

<hs>  The prevalence of low wealth in late life</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The upper panel of Fig. 1 shows the cumulative distribution of total wealth ($000 s) and
of financial assets ($000 s) from the last survey wave prior to death for the 7848 HRS
respondents over the age of 65 who died during our sample period. The figure shows the
distribution for individuals, both married and single, with balances between -$50,000 and
$1,000,000. We excluded 554 respondents with wealth values outside this range. Among those
who died, the median wealth when last observed was $115,000 ($2012). More than three-
quarters of respondents had financial assets less than that value. Four percent (including
persons with balances less than −$50,000) had negative net worth, and 7% reported net
worth of zero. About 8% of those who died were in households with negative financial
assets, inclusive of 401(k) and IRA balances; 14% reported a zero balance. The median
financial asset balance was $18,500. Most decedents were in households with relatively
limited financial assets. The lower panel focuses on the 1073 married individuals who are
in the longitudinal sample. The distribution is similar to that in the upper panel, but
the respondents in the longitudinal sample have somewhat higher wealth at most quantile
rankings. This is largely because the longitudinal sample is limited to married
individuals, and married individuals on average have more wealth than elderly singles.
Defining “low wealth” as wealth below $100,000 would include roughly half of the decedents
in our sample. Somewhat arbitrarily, we use two definitions of “low wealth”: wealth less
than $100,000 and less than $50,000. We also consider two measures of low financial
assets: less than $50,000 and less than $25,000. In our full sample, 46.5 (33.8) percent
of decedents fell below the $100,000 ($50,000) total wealth threshold. The low level of
wealth for many households in their later years is not unique to the United States.
Atkinson and Sutherland (1993) report that in the U.K., a substantial fraction of elderly
households has little wealth and no private retirement support, and are therefore depends
primarily on public support.

<hs>  The evolution of wealth at older ages</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The rate at which households draw down their wealth after retirement has long been an
active research question. Particular attention for public policy purposes focuses on
whether some individuals draw down their wealth rapidly after retirement, reaching old age
with very limited wealth holdings. Fig. 2 plots the three-year moving average of the age-
specific wealth of all HRS respondents (upper panel) and the married respondents who
constitute the longitudinal sample. The figure shows average household wealth, in $2012,
of all HRS individuals of a given age in any year of our data sample. The figures show the
mean level of wealth, which is sensitive to the top wealth households, and the 25th, 50th
and 75th quantiles. The slope of the profiles reflects both age and cohort effects, since
those who older are, on average, from cohorts that were born earlier and had less lifetime
income than their younger counterparts. The upper panel suggests gradual wealth decline,
perhaps with slight acceleration in the decline as respondents age. Mean wealth declines
by more than $100,000 between ages 65 and 75, but the rate of decline in wealth is much
slower than the rate of decline in remaining life expectancy. The absolute rate of decline
is greatest for the mean and 75th percentile wealth holdings. For example, the mean ratio
(wealth at 80/wealth at 65) is 0.81. This value is 0.80 at the 75th percentile, 0.84 at
the 50th, and 0.92 at the 25th percentile of the wealth distribution. Fig. 2 suggests
relatively modest wealth decline at each point in the distribution that we consider.
Second, there is a substantial group of individuals – at least those up to the 25th
percentile – who have very low wealth holdings throughout the retirement period. The
second panel in Fig. 2 shows wealth holdings for the individuals followed from age 65 to
death. There is a notable difference between upper and lower panels: there is almost no
downward slope for individuals in the lower panel. This is true for the mean and for all
of the quantiles we consider. This raises the possibility that a mixture of cohort and age
effects in the figure confounds estimating the age pattern of draw-down. One factor that
may confound the wealth-age profiles is housing equity. Previous studies, such as Venti
and Wise (2004), have found that older households are slow to move from the homes that
they have lived in for many years, and that they are also reluctant to tap the equity in
their homes to support other consumption. It is therefore possible that the age-financial
assets profile might differ from the age-wealth profile, particularly given the importance
of housing equity in the portfolios of older households. Fig. 3 addresses this issue. The
upper panel shows the average financial assets of HRS respondents of each age, and the
lower panel presents comparable information for the “longitudinal” sample of married
individuals who die during the sample period. The results are very similar to those in
Fig. 2: for the full HRS sample, there is a clear negative slope to the age-financial
assets profile for the median and the 75th percentile financial asset value. The lower
quantiles are much more stable across ages. For the longitudinal sample, there is very
little change between age 65 and age 79 in the level of financial assets. These results
also suggest that the negatively-sloped age-wealth profile from the simple tabulations may
be spurious. Fig. 4 shows the three-year moving average of the estimated age coefficients
(γi) from Eq. (1) for specifications in which total wealth and financial assets are the
dependent variable. The age-wealth profile for total wealth shows some decline with age,
but the decline is much more gradual than for the full sample age-wealth profile in Fig.
2. The decline in average wealth between ages 65 and 88 in Fig. 4 is about one quarter the
decline in Fig. 2. For financial assets, the wealth decline in Fig. 4 is much less
pronounced than that in Fig. 3. This suggests that part of the declining age-wealth
profile in simple HRS tabulations is due to time effects that confound the age profile.
This factor appears to dominate the countervailing effect of dynamic sample selection:
individuals in higher socio-economic strata live longer on average, so the survivors at
older ages is disproportionately drawn from higher wealth individuals. This would lead to
a positive bias between age and the measured wealth effects, since the lower wealth
members of a given birth cohort would be likely to die at younger ages, imparting a
positive bias to the slope of the age-wealth profile. Our findings provide new evidence on
the decades-long debate about the extent to which the accumulation and draw-down pattern
suggested by simple life cycle models can characterize observed age-wealth profiles. The
finding of relatively slow drawdown of total wealth – from an average of about $550,000 at
age 65 to less than $500,000 by age 88 – is consistent with models in which retirees are
husbanding their resources for potential late-life expenses than with models in which they
are drawing down assets as soon as they reach retirement age. It supports a number of
earlier studies, including Blundell et al. (2016), DeNardi et al. (2016), and Love et al.
(2009), that find relatively slow draw-down of wealth after retirement. These results
underscore the importance of including bequest motives, precautionary saving motivated by
stochastic late-life expenditure needs, or other factors that can rationalize the slow
draw-down of wealth in models that explain post-retirement wealth dynamics.

<hs>  Determinants of wealth at retirement</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The relatively modest age-related changes in wealth that the foregoing figures exhibit
suggest that the distribution of wealth near the end of life may be largely determined by
wealth at age 65. We now turn to its determinants. Table 1a reports the fraction of
individuals in households with total wealth below either $25,000 or $100,000 at age 65,
and it summarizes how the probability of falling in these low wealth categories varies
with lifetime earnings and education. Among married 65-year olds, 9.3 (22.4) percent have
household wealth less than $25,000 ($100,000). The fractions of single persons below each
threshold are greater, 39% and 57.5% respectively. The wealth a household has accumulated
by age 65 depends on its lifetime labor income as well as decisions about how much to save
and how that saving was invested, which affects the rate of return it has earned. Table 1a
stratifies the age-65 population in three ways: by education, by the presence or absence
of a pre-retirement health condition, and by lifetime earnings quintile. Each of these
factors may affect retirement wealth. Regardless of whether low wealth as defined using
the $25,000 or $100,000 threshold, the variation across range across levels of education
is similar to the range across lifetime earnings quintiles. For example, using the $25,000
threshold for married persons, about 23% of those in the lowest education group and 3% of
those in the highest fall into this “low wealth” category. The pattern is similar for
singles. Table 1b presents tabulations similar to those in Table 1a, but for financial
assets. Single individuals have, on average, less wealth and fewer financial assets than
those in married couples. Nearly 57% of single persons have household financial assets
less than $10,000 at age 65, compared with 28.8% of individuals in married couples.
Similarly, 68.2% of singles have less than $50,000 of financial assets, compared with
44.5% for married individuals. Table 1b shows that the percentage of persons with low
financial assets varies dramatically by lifetime earnings quintile and by level of
education. Using the $10,000 threshold, married persons in the lowest education group are
7.5 times more likely to have low financial assets than those in the highest education
group. Married individuals in the lowest lifetime earnings quintile are 5.7 times more
likely to have low financial assets than those in the highest quintile, and those in the
lowest education and earnings quintiles are 16.1 times more likely to have low financial
assets that those with high education and earnings. Education may have an indirect
association with wealth at retirement through the effect of education on lifetime
earnings. However, education also has an association with wealth that is independent of
lifetime earnings. Within each earnings quintile, there are sharp differences in the
probability of reporting low wealth. For married persons in the highest earnings quintile,
for example, the probability of reporting less than $10,000 in financial assets is 32% for
those with less than a high school degree, compared with 5% for those with at least a
college degree. These differences could reflect a direct effect of education on saving
rates and retirement preparation, such as an effect of education on financial literacy, or
a spurious correlation between time preference rates and educational attainment that is
manifest in different levels of retirement wealth. Tables 1a and 1b also explore the
relationship between the pre-retirement onset of a major health condition and the
likelihood of reaching retirement age with low wealth. For married persons, the
probability of reporting low wealth is higher for those who experienced a major health
condition. For example, using the $25,000 threshold (top panel of 1a), 7.6% of those who
did not experience a major health condition had low wealth, compared with 12% of those who
did. For singles, the percentage below the $25,000 threshold is 32.8% for those who did
not experience a major health event and 48.3% for those who did. Not only is the
probability of falling below this threshold higher for singles, the derivative effect of
poor health for singles is larger than for married individuals. This casts doubt on the
empirical significance of intra-household insurance mechanisms against chronic health
shocks and other financial difficulties. Across lifetime earnings quintiles, the
differences in the probability of reporting low wealth conditional on a health issue, even
conditioning on lifetime earnings quartile, suggest that the effect of poor health on
retirement wealth is not due only to its impact on earnings. Poor health can lead to
reduced labor supply as well as higher levels of health-related spending. Dobkin et al.
(2018), using several merged administrative data sets, find that hospitalizations among
those under 65 are associated with reduced earnings and elevated debt levels. Our findings
are supportive, and suggest that even after conditioning on lifetime income quantile,
there are negative effects of a chronic health condition on wealth at retirement. This
underscores the possibility of a non-earnings channel, such as out-of-pocket medical
expenses that draw down wealth.

<h>WEALTH DYNAMICS: FROM AGE 65 TO THE END OF LIFE</h>
-----------------------------------------------

The slow rate of post-65 wealth decline suggested by the foregoing figures implies that
wealth at 65 is likely to be a key determinant of wealth at the end of life. We now
explore this relationship in more detail, first comparing wealth at 65 and at the end of
life in repeated HRS cross sections, and then studying the subset of respondents who are
observed both at age 65 and just before death.10

<hs>  Repeated cross-section evidence</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

3546 HRS respondents have linked earnings histories and are observed either at age 65 or
66. 2841 respondents have linked earnings histories and who die within our sample period.
We can compare the wealth at retirement and wealth when last observed of these two groups
– which have 1073 married respondents in common – to explore the differences between
wealth at retirement and at death. Table 2 reports these comparisons. More HRS respondents
have less than $100,000 in total wealth in the last survey before death than at age 65.
For married individuals, the chance at age 65 of having wealth (financial assets) below
$100,000 ($50,000) was 22.4 (44.5) percent. We reject the null hypothesis of an equal
percentage of respondents below these thresholds at 65 and when last observed at the 95%
confidence interval for the whole sample and for several subgroups stratified by lifetime
earnings.11 The same pattern, but weaker statistical significance, is observed for
singles. For some subgroups reported in Table 2, the probability of low wealth is higher
at retirement than at death, but the null hypothesis of equality is only rejected in one
of these cases. Most individuals who report low late-life wealth were also low lifetime
earners. Nearly half – 47.8% – of the married individuals with wealth of less than
$100,000 in the last survey before death were in the lowest quintile of lifetime earnings,
as were 40.1% of those with less than $100,000 of total wealth at age 65. The pattern is
similar for financial assets: 40.7% of those with less than $50,000 in financial assets at
death were in the lowest lifetime earnings quintile; 31.5% of those with this level of
financial assets at retirement were in the lowest earnings quintile. These data suggest
that low lifetime earnings are a key predictor of low wealth at both retirement and end-
of-life.

<hs>  Evidence from HRS cohorts, retirement through death</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The entries in Table 2 compare individuals at age 65 and at the end of life, but
relatively few of the individuals in these two samples – 1073 married and 481 single
respondents – are observed at both 65 and at the end of life.12 To provide longitudinal
information on wealth trajectories, we now focus on this subsample of married individuals,
and explore the relationship between wealth at 65 and at the end of life. We caution that
this sample disproportionately includes individuals who died at young ages, because our
sample spans only 16 years. No one in this longitudinal sample died at an age beyond 82.
Our findings thus apply to the draw-down patterns of the “young elderly” but may not
generalize to older groups. Fig. 5 graphs total wealth at age 65 and total wealth at death
for the longitudinal sample; it shows only the 932 individuals with total wealth less than
$1,000,000 at each date. The number of years that elapse between the two wealth
measurements can be anything from two years for those who die in their mid-60s to nearly
16 years for those who die in 2012 and who were first surveyed in 1996. Those with flat
trajectories of wealth in retirement will fall close to the 45-degree line. The figure
shows substantial numbers of respondents with trajectories that place them above or below
the 45-degree line. There percentage for whom the difference between the two wealth values
exceeds $100,000 is relatively small, however: 30.8%. At low levels of wealth, most
individuals are close to the 45-degree line, suggesting little change in wealth holdings
between age 65 and the last HRS observation before death. Wealth declined for 54.9% of the
longitudinal sample, was recorded as zero in both surveys for 1.0%, and increased for
44.1%. One shortcoming of the longitudinal sample is that the maximum number of years
between age 65 and the last wave before death is about 14 years, so we are not observing
wealth trajectories for those who die after age 79. It is likely that if we had
longitudinal data for an even longer period, we would observe larger differences between
wealth at age 65 and at death. Measurement error may explain some of the wealth movements
that we observe. Wealth is self-reported and accurate reporting of a household's financial
circumstances is a challenging task that may become more difficult as respondents age and
cognitive skills decline. Researchers have long recognized the potential for measurement
error to confound studies of household wealth, particularly when the analysis focuses on
wealth differences. Hill (2006), Venti (2011), and Meijer et al. (2013) all report
evidence of significant measurement error in the HRS, but none offer suggestions for
resolving it nor a calibration that would enable us to assess the potential impact on our
results. For example, Hill (2006) finds that call-back verification reduced the variance
of wave-to-wave asset changes about 50%. Hurd et al. (2016) demonstrate that greater
cross-wave validation effort reduces the variation across waves and improve the quality of
data imputation. The HRS data file that we analyze incorporates the insights of this
analysis. We focus our empirical strategy on measures of whether wealth falls below a
threshold value in part to reduce the impact of measurement error. For respondents whose
true wealth value is far from the threshold, even a large and transitory measurement error
in one year will not bump the respondent across the low-wealth indicator. Tables 3 and 4,
which present core transitions between wealth at age 65 and wealth when last observed
before death. The top panel shows the percentage of married persons in various total
wealth intervals at age 65 who were in various intervals when last observed. The off-
diagonal entries reflect movements in wealth or financial assets. For example, 31.7% of
the respondents who reported between $10,000 and $50,000 of total wealth at age 65 were in
this same wealth category at death. There is greater persistence in the top and bottom
categories: 73.6% of those who reported less than $10,000 in wealth at age 65 were in this
wealth interval in the survey before death; 76.7% of those with more than $250,000 in
assets at age 65 were similarly categorized when last surveyed. Some individuals make
significant transitions in wealth holdings. 7.4% of those who reported more than $250,000
at age 65 had less than $100,000 when last surveyed. While we would like to explore what
happened to the respondents in this group, the number of respondents with large declines
is too small. The patterns are broadly similar for financial assets (lower panel), and if
anything, low values are more persistent in that case. Table 4 reverses the conditioning:
it stratifies married individuals in various total wealth intervals in the last year
observed before death by their reported wealth at age 65. It shows column percentages
rather than the row percentages shown in Table 3. For example, 48.2% of those last
observed with less than $10,000 of total wealth also had less than $10,000 of total wealth
at age 65. Persistence is particularly strong for persons dying with substantial wealth:
81.6% of those who have more than $250,000 when last observed also had more than $250,000
at age 65. At low wealth levels, of those with less than $10,000 of total wealth at death,
18.6% had more than $100,000 entering retirement, while over 50% of those with between
$10,000 and $50,000 of wealth when last observed had wealth of more than $50,000 at age
65. This suggests some “downward mobility” between age 65 and death among those who had
accumulated substantial assets at retirement. The bottom panel of Table 4 suggests similar
patterns for financial asset mobility.13 Tables 3 and 4 suggest that about one third of
those who are observed with low wealth at death entered this state between age 65 and
death. While large movements in wealth or financial assets between age 65 and death are
relatively uncommon for those who die before the age of 80, there are some households that
draw down their assets and are poorer at death than at they were at retirement age. Most
of those with low wealth at death, however, had low wealth at retirement.

<h>HEALTH SHOCKS, SPOUSAL DEATHS, AND POST-RETIREMENT WEALTH TRAJECTORIES</h>
----------------------------------------------------------------------

We now examine two potential shocks – the onset of a health condition and death of a
spouse - that could lead some individuals to fall into the low-wealth category. We in
particular ask if these shocks could explain the wealth trajectory of the subset of HRS
respondents who did not have low wealth at age 65, but did at the time of death.

<hs>  Adverse health events</hs>
  ~~~~~~~~~~~~~~~~~~~~~

The probability of ever having experienced a major health condition – cancer, heart
disease, lung disease, or stroke – rises as individuals age. In our HRS sample, this
probability is about 35% at age 65. It is nearly 65% by age 90. The probability of
experiencing one of these conditions for the first time rises from about 5% per two-year
interval (between HRS waves) at age 65 to between 6 and 7% at ages above 80. It is
relatively stable for individuals of the ages we consider in our longitudinal sample. We
explore the association between the onset of a major health condition and low wealth on
the eve of death by comparing the wave-to-wave change in the probability of low wealth for
those first reporting the onset of a major health condition to the wave-to-wave change for
those who have never experienced any major health condition. The “never experienced” group
is one of several comparison groups that could be used for this analysis; it is attractive
because it does not raise confounding issues about the lagged effect of past major health
conditions. There are 3832 respondent-years for our married person sample in which a new
health condition is reported, and 17,063 respondent-years in which a survey participant
who has never reported a major condition.14 Including a set of indicator variables for the
level of educational attainment controls for the variation in the baseline risk of
reporting low wealth that is education-related. Table 5 presents the results of estimating
Eq. (2). The onset of a major medical condition is associated with an increase of about
0.8 percentage points in the chance that total wealth is below $25,000 for married
individuals. The point estimates of the effects are larger but less precisely estimated
for singles and we do not reject the null hypothesis of no effect. We also estimated
effects over longer time periods – two and three waves – for both married and single
respondents, and found that the standard errors rose and we could not reject the null
hypothesis of no effect. Our analysis differs from the many previous studies that focus on
the change in wealth at the time of a new health condition in that we focus on the
likelihood of reporting low wealth, which as we explained at the outset, is particularly
relevant for a number of policy issues.

<hs>  Death of a spouse</hs>
  ~~~~~~~~~~~~~~~~~

Fig. 6 reports the percent of married persons in the HRS over the age of 65 in each wave
whose spouse died before the next wave. The horizontal axis is the age of the surviving
spouse at the beginning of the two-year interval. Women tend to have older spouses and men
tend to have younger spouses, so the age at which one partner becomes a widow/widower (on
the horizontal axis) may be an imperfect indicator of the age of the partner at their
death. The probability that a partner will die in a two-year interval increases from about
2% at age 65 to a little over 3% at age 70 and to almost 9% by age 80. Table 6 reports a
specification similar to that in Eq. (2), but the central explanatory variable of interest
is now the death of a spouse between wave t-1 and wave t. These estimates use a longer
sample, but a similar approach, to the study by Sevak et al. (2003). The findings suggest
that when a husband dies, the probability that his wife will report total wealth below
$100,000 rises by about 1.6 percentage points, and the probability that she will report
wealth below $25,000 rises by about 2 percentage points. For men, we do not reject the
null hypothesis that the loss of a spouse has no effect. Some point estimates for
financial assets, although none that are statistically significantly different from zero,
suggest that loss of a spouse is associated with a rise in financial assets. Could there
be any circumstances under which this might occur? Death-related payouts, such as life
insurance benefits could lead to this outcome, especially because even a modest payout
could move someone out of the low-wealth status. Financial assets could also rise if
caring for a declining spouse leads to sale of a house and an associated set of balance
sheet transfers. We explored the role of life insurance, and did not find any consistent
evidence that the survivors of spouses with insurance were more likely to exit the low
wealth state than the survivors of uninsured spouses. Even for the survivors of spouses
without insurance, there were some reductions in the probability of reporting low wealth.
We also explore the relationship between changes in wealth between age 65 and death, and
new health conditions or the death of a spouse, in our longitudinal sample. 59.1% of those
who experienced a major new health condition between age 65 and death reported a decline
in wealth, compared with 52.7% of those who did not report but died within the sample.
This difference is statistically significantly different from zero. For financial assets,
the values are 59.2 and 54.2%, with a t-statistic of 1.58 for the difference. 63.2% of
those who lost a spouse and also died within the sample reported a decline in wealth
between 65 and death, compared with 54.3% of those who died but did not report losing a
spouse (this difference is also statistically significantly different from zero).
Reversing the conditioning, among those who experienced a decline in wealth (financial
assets) between age 65 and death, 45.7% (45.4%) were diagnosed with a new health
condition. This corresponds to 39.3% (40.5%) for those whose assets increased. Those whose
wealth declined were also more likely (14.6 vs 10.6%) to have lost a spouse (t-statistic
of 1.98). These findings do not control for potential differences between the various
groups, but they suggest that there may be cumulative effects of both adverse health
shocks and loss of a spouse.

<h>CONCLUSIONS</h>
-----------

Low lifetime wealth accumulation, which results in low wealth at retirement, is the most
important factor contributing to low wealth in late life. Nearly two thirds of HRS
respondents who were observed both at age 65, and about one year before their death, and
who had net worth of less than $50,000 at death, also had similarly low wealth levels at
age 65. Lifetime earnings and educational attainment are important determinants of wealth
at age 65, and education is strongly correlated with wealth even after controlling for
lifetime earnings. Just over 50% of high school graduates have low wealth, compared with
only 6.4% of those with a college degree. Forty-five percent of married persons in the
lowest quintile of the distribution of lifetime earnings have net worth of less than
$100,000 at age 65, compared with only 7% of those in the highest quintile. These findings
document an association but do not explain the mechanism linking education and wealth at
retirement. One possibility is that education increases awareness of the need to save, or
it makes individuals wiser investors who can earn a higher rate of return on their
savings. Reverse causality is another possibility: those with more education may have
wealthier parents and may have received larger bequests or other transfers. Still another
possibility is that some third factor, perhaps time preferences, may have similar effects
on financial and educational investments, inducing the strong positive correlation between
education and wealth. Identifying a causal mechanism underlying the strong association
merits further attention. In contrast to concerns that some households will draw down
their retirement wealth at a rapid rate in the years following retirement, and exhaust
their wealth before they die, we find relatively few households dropping to low wealth at
death from modest wealth at retirement. In our longitudinal sample, 34.3% of married
persons had wealth of less than $100,000 at age 65, compared with 40.1% just prior to
their death. 67.1% had financial assets worth less than $50,000 at retirement, compared
with 70.1% just prior to death. 55% reported lower wealth at death than at retirement.
Both a decline in health, and the loss of a spouse, raise the likelihood of reporting low
wealth, but the effects are modest. Onset of a major health condition is associated with
an increase in the fraction of married persons with wealth below $100,000 from 21.3 to
23.8%. Death of a spouse is associated with a rise from 29.7 to 30.9%. The findings
regarding health shocks are consistent with the view, described for example in Barcellos
and Jacobson (2015) and Dobkin et al. (2018), that Medicare protects most of the over-65
population from substantial burdens associated with health shocks. This may be
particularly true for those low in the wealth distribution. Poterba and Venti (2017) find
that the negative wealth effects of three health-related shocks – hospitalization,
admission to a nursing home, and use of a home health aide – are all much greater for
those with net worth above $500,000 than for those with net worth below $100,000. This can
reconcile the possibility that wealth declines, on average, in response to these shocks,
while there is only a small effect on the probability of falling into low wealth.
Households near the low wealth threshold may experience relatively less draw-down in
wealth in response to these shocks than those higher up in the distribution. We have
implicitly treated health shocks as creating mandatory expenditure needs that must be met,
but there is another channel through which such shocks could influence the draw-down of
wealth. Households experiencing such shocks might change their spending patterns, and
hence their wealth trajectories. If adverse health events cause individuals to reduce
their estimate of their longevity, they might respond by increasing their consumption
spending and the rate at which they draw down wealth. Because the change in wealth
reflects the return on wealth, plus other income, less consumption and health
expenditures, an increase in consumption would appear as a decline in wealth for those
experiencing adverse health shocks. Exploring competing mechanisms for the wealth health
linkage is a topic for future work. Most of our results are based on a sample of
individuals who died before age 80. It is possible, as Lee and Kim (2008) argue, that
adverse health shocks at later ages are costlier than similar shocks at younger ages. More
generally, wealth dynamics at older ages may differ from those at younger ages. As longer
HRS longitudinal samples become available, it will be possible to extend our findings;
they may change.


<h>REFERENCES</h>
----------

  [1] Facundo Alvaredo, Anthony B. Atkinson, Salvatore Morelli. The Challenge of Measuring UK Wealth Inequality in the 2000s. doi:10.1111/j.1475-5890.2016.12084
  [3] A. B. Atkinson. The distribution of wealth and the individual life-cycle. doi:10.1093/oxfordjournals.oep.a041192
  [5] Silvia Helena Barcellos, Mireille Jacobson. The effects of medicare on medical expenditure risk and financial strain. doi:10.1257/pol.20140262
  [6] Richard Blundell, Rowena Crawford, Eric French, Gemma Tetlow. Comparing Retirement Wealth Trajectories on Both Sides of the Pond. doi:10.1111/j.1475-5890.2016.12086
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  [9] Mariacristina De Nardi, Eric French, John Bailey Jones. Savings after Retirement: A Survey. doi:10.1146/annurev-economics-080315-015127
  [10] Carlos Dobkin, Amy Finkelstein, Raymond Kluender, Matthew J. Notowidigdo. The Economic Consequences of Hospital Admissions. doi:10.1257/aer.20161038
  [12] Daniel H. Hill. Wealth dynamics: Reducing noise in panel data. doi:10.1002/jae.878
  [14] Amy S. Kelley, Kathleen McGarry, Rebecca Gorges, Jonathan S. Skinner. The burden of health care costs for patients with dementia in the last 5 years of life. doi:10.7326/M15-0381
  [15] Jinkook Lee, Hyungsoo Kim. A longitudinal analysis of the impact of health shocks on the wealth of elders. doi:10.1007/s00148-007-0156-5
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<ART>Macroeconomic effects of fiscal adjustment: A tale of two approaches
====================================================================

Authors: Weonho Yang, Jan Fidrmuc, Sugata Ghosh
DOI: 10.1016/j.jimonfin.2015.05.003
Year: 2015  |  Pages: 31-60
ASJC codes: 2002, 2003
Keywords: Cyclically adjusted primary balance, Fiscal adjustment, Fiscal policy, Narrative approach

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We investigate the short-term effects of fiscal adjustment on economic activity in 20 OECD countries from 1970 to 2009. We compare two approaches: the traditional approach based on changes in cyclically adjusted primary balance (CAPB) and the narrative approach based on historical records. Proponents of the latter argue that it captures discretionary fiscal adjustment more accurately than the traditional approach. We propose a new definition of CAPB that takes account of fluctuations in asset prices and reflects idiosyncratic features of fiscal policy in individual countries. Using this new definition, we find that fiscal adjustments always have contractionary effects on economic activity in the short term; we find no evidence of expansionary (non-Keynesian) fiscal adjustments. Spending-based fiscal adjustments lead to smaller output losses than tax-based fiscal adjustment. These results are in line with the literature using the narrative approach, suggesting that the CAPB, when correctly specified, can be used as a measure of fiscal adjustments.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The recent global economic and financial crisis and the associated fiscal austerity in the
Eurozone and elsewhere have resulted in a renewed interest in the relationship between
fiscal reform and economic growth. Although there is widespread agreement that reducing
public deficits and debt has important benefits in the long term, there is less of a
consensus regarding the short-term effects of fiscal adjustment. In part, this is because
of the oft-quoted examples of Denmark and Ireland, which experienced improved growth
performance after periods of strict fiscal austerity in the 1980s.1 Their experience
defies the conventional Keynesian theory which predicts negative short-run economic
effects of restrictive fiscal policy. Subsequently, Giavazzi and Pagano (1990), Alesina
and Perotti (1997), Alesina and Ardagna (1998, 2010) and others sought to find other
examples of such expansionary fiscal adjustments and argued that fiscal adjustment can
stimulate economic growth even in the short term, in a phenomenon referred to as ‘Non-
Keynesian effects’ or ‘expansionary fiscal contraction’. Typically, the empirical studies
seeking evidence of expansionary fiscal adjustments rely on observing changes in the
cyclically adjusted primary balance (CAPB). The CAPB is an indicator that captures
discretionary fiscal policy and other noncyclical factors by excluding the automatic
effects of business cycle fluctuations (through transfers, taxes and interest payments) on
the budget.2 However, Guajardo et al. (2014) criticize this approach on the grounds that
using the CAPB can yield misidentified fiscal adjustment episodes. In particular, they
argue that improvements in the CAPB due to stock-market booms and/or one-off fiscal
revenues can be misclassified as fiscal reforms. They favor a narrative approach, based on
careful study of historical documents to identify fiscal adjustments episodes. Applying
this to a sample of OECD countries, they fail to identify any expansionary fiscal
adjustments. In this paper, we build on and extend the work of Guajardo et al. (2014). We
consider 20 OECD countries so that our scope is similar to that of their paper. In
contrast to their approach, we use the CAPB instead of the narrative approach. However, we
modify the CAPB to take account of the problems that Guajardo et al. (2014) point out. In
particular, we construct the CAPB measure so that it reflects fluctuations in asset prices
and takes into account the heterogeneity of fiscal policy across countries. Using this new
measure of fiscal adjustment, we obtain results that are very similar to those that
Guajardo et al. (2014) obtain with the narrative approach. With our modified CAPB measure,
we find no evidence of Non-Keynesian effects. Nevertheless, our results confirm that
spending-based fiscal adjustments have more beneficial macroeconomic effects than tax-
based fiscal adjustments, which is in line with the previous theoretical and empirical
evidence. This paper is organized as follows. Section 2 reviews the theoretical and
empirical literature on the effects of fiscal adjustments. In section 3, we explain our
new measure to identify fiscal adjustments and list the fiscal adjustment episodes that we
identify. Section 4 outlines the empirical framework and presents the results. Section 5
examines the robustness of our results. Finally, section 6 concludes.

<hs>  Theory</hs>
  ~~~~~~

There is a general agreement that fiscal consolidation and the resulting reduced
government debt contribute to long-run economic growth. However, there is disagreement
about the short-term effect. Keynesian economics predicts that a cut in government
spending or an increase in taxes reduces the aggregate demand and income directly, which
leads to negative multiplier effects on the output in the short term. As a result,
government debt to output ratio may not be reduced much or at all because both output and
tax revenues fall due to the contractionary effects of the fiscal adjustment. In contrast,
Neoclassical economics predicts that fiscal adjustments can stimulate the economy with an
increase in private consumption and investment through several transmission mechanisms
even in the short term. These mechanisms entail both demand and supply side effects.
First, on the demand side, wealth effects or credibility effects are suggested to be at
work. Blanchard (1990) proposes a model in which consumers react to two kinds of effects.
One is the intertemporal tax redistribution effect by non-Ricardian agents in a Keynesian
model where an increase in taxes decreases consumption. The other is due to distortionary
effects of taxes, whereby an increase in taxes eliminates the need for a larger and more
disruptive adjustment in the future. As a result, people can expect an increase in their
permanent income due to the future reduction in the deadweight loss, and therefore consume
more. Blanchard argues that if people exhibit little myopia and the fiscal adjustment is
made from a high debt level, consumption can react positively. Bertola and Drazen (1993)
present an optimizing model and demonstrate that if a change of fiscal policy induces
sufficiently strong expectation of future policy change in the opposite direction, it can
give rise to a nonlinear relationship between private consumption and government spending.
If a cut in government spending induces expectation of significantly lower future taxes,
it may induce an increase in the current private consumption. Similarly, Sutherland (1997)
links current fiscal policy and future expected taxes. His model emphasizes the dynamics
of government debt and considers consumers with finite horizons. At low levels of debt,
fiscal policy has the usual Keynesian effects because people expect the debt stabilization
program as something distant from their perspective. On the other hand, at high levels of
debt, as a major fiscal consolidation is imminent, people react to government spending in
a non-Keynesian way, expecting that they will have to pay more taxes shortly. Therefore,
fiscal adjustment can give rise to positive wealth expectation effects when it occurs
under high and rapidly growing debt-to-GDP ratio. Other mechanisms include credibility
effects, whereby fiscal adjustment reduces the default and inflation risk via the decline
in interest rates (Feldstein, 1982). When a high level of government debt affects the
interest rate risk premium, a reliable fiscal adjustment can reduce the premium and, in
turn, the reduction of interest rate raises permanent income. In addition, lower interest
rate can also lead to the appreciation of financial assets which triggers higher
consumption and investment. Expansionary fiscal adjustment may take place also on the
supply side via the labor market and investment (Alesina et al., 2002, 2008). If fiscal
adjustment takes the form of a cut in public spending, especially in the area of public
employment, rather than an increase in taxes, it can lead to a reduction of overall wage
pressure in the economy and stimulate private employment and investment.

<hs>  Empirical considerations</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~

There is a large empirical literature seeking to find evidence of expansionary fiscal
adjustments (non-Keynesian effects) since Giavazzi and Pagano (1990) suggested, based on
the examples of Denmark and Ireland in the 1980s, that large and decisive fiscal
adjustment can increase private consumption. Fiscal adjustment is usually identified as an
improvement of CAPB in excess of a chosen threshold over a given period. Two aspects of
fiscal adjustments receive attention: the factors that ensure that fiscal adjustments are
expansionary or successful, and the effects of fiscal adjustments on macroeconomic
outcomes. The studies interested in the former classify the episodes according to the
definition of expansionary or successful fiscal adjustment3 and then perform a descriptive
analysis of the characteristics of fiscal components and other related macroeconomic
variables such as GDP and interest rate before, during, and after the fiscal adjustment
period (Alesina and Ardagna, 1998, 2010, 2012; Alesina and Perotti, 1995, 1997; Giudice et
al., 2007; McDermott and Wescott, 1996). These studies tend to find that fiscal
consolidations based on spending cuts rather than on tax increases are more likely to be
both expansionary and successful. Other papers use binary dependent variable models such
as logit or probit to analyze which factors determine the success of fiscal consolidations
(Afonso et al., 2006; McDermott and Wescott, 1996) and their expansionary effects (Alesina
and Ardagna, 1998; Giudice et al., 2007). McDermott and Wescott (1996) argue that the
success in reducing the debt ratio depends on the size and composition of fiscal
adjustment. They show that fiscal adjustments based on spending cuts are more likely to be
successful than tax-based ones. Furthermore, the greater the magnitude of fiscal
adjustment, the more likely it is to succeed. On the other hand, they show that fiscal
adjustments are more likely to fail during a global recession. Afonso et al. (2006) assess
fiscal consolidations in Central and Eastern European countries and suggest that spending-
based adjustments were more successful. Giudice et al. (2007), finally, conclude that
fiscal consolidation is more likely to promote economic growth during periods of below
potential output and when the fiscal adjustment is based on spending cuts. The latter
focus (on macroeconomic effects of fiscal adjustments) is less common. Using panel data of
industrial and developing countries, Giavazzi et al. (2000) analyze the relationship
between fiscal policy and national savings and conclude that their relationship can be
nonlinear when the fiscal impulse is sufficiently large and persistent, similar to the
previous studies on fiscal policy and private consumption (Giavazzi and Pagano, 1990,
1996). Ardagna (2004) studies the determinants and channels through which fiscal
adjustment affect growth. She shows that whether a fiscal adjustment is expansionary
depends largely on the composition of fiscal policy, and that spending cuts can lead to
higher growth rates via the labor market rather than through agents' expectation. On the
other hand, Burger and Zagler (2008) analyze the relation between U.S. growth and fiscal
adjustments in the 1990s and argue that non-Keynesian effects prevail through an increase
in consumption because of improved consumer confidence and an increase in investment via
the labor market and financial market. Afonso (2010) assesses expansionary fiscal
adjustment in European countries and finds that fiscal consolidations tend to have long-
term expansionary effects, but no significant effects in the short-run. Thus, although
there are some differences among these empirical studies in the factors affecting
expansionary fiscal adjustment such as the size, composition and the initial conditions,
overall, the empirical literature based on fiscal adjustment episodes identified by the
changes in the CAPB supports the existence of non-Keynesian effects. Several papers,
however, take issue with the results of the aforementioned CAPB-based studies. First, they
argue that the results can be plagued by selection bias, measurement error, spurious
correlation, or simultaneity issues when identifying fiscal consolidation episodes. Using
the same panel data as Giavazzi et al. (2000), Kamps (2006) challenges their finding that
non-Keynesian effects are a general and easily exploitable phenomenon by showing that the
nonlinear effect disappears when cross-country heterogeneity is taken into account. Park
and Song (2010) and Hernández de Cos and Moral-Benito (2011) raise the possibility of
endogeneity of the fiscal consolidation decision and find that fiscal adjustments have
negative effects on GDP when taking this into account. In line with these criticisms, IMF
(2010), Guajardo et al. (2014) and Devries et al. (2011) suggest an alternative way of
identifying fiscal consolidations instead of using the CAPB. Their approach is based on
reviewing historical documents, similar to Romer and Romer (2010), to identify
discretionary fiscal changes motivated by the desire to reduce the budget deficit. They
then compare their episodes with those of Alesina and Ardagna (2010) and show that the
episodes identified using historical data have contractionary effects on GDP, while the
CAPB-based episodes are associated with a rise in GDP. Hence, using the CAPB is likely to
be biased in favor of non-Keynesian effects. The narrative literature, furthermore,
identifies a number of problems related to using the CAPB. First, using a statistical
concept such as the CAPB can be marred by non-policy related developments such as booms or
contractions in the stock market.4 Second, the CAPB-based method is likely to ignore the
motivation behind fiscal changes. For example, the rise of CAPB can be aimed at
restraining economic overheating, not at reducing the budget deficit.5 In addition, it can
omit some episodes of fiscal adjustment followed by an adverse shock and discretionary
fiscal stimulus.6 Third, the CAPB data cannot exclude some cases of offsetting positive
changes in the CAPB caused by large one-off accounting operation in the previous year that
are unrelated to fiscal adjustment measures, such as the capital transfers of Japan in
1998 and the Netherlands in 1995.7 Based on their new dataset, they conclude that fiscal
adjustments have contractionary effects on economic activity, and argue that large
spending-based fiscal consolidations cannot be expansionary. On the other hand, Alesina
and Ardagna (2012) re-estimate the effect with new episodes identified based on the
persistence of CAPB changes rather than on their size. They make a somewhat intermediate
conclusion that spending-based adjustments cause smaller recessions than tax-based ones.
They also argue that an expansionary fiscal adjustment is possible when it is combined
with accommodating monetary policy. Last but not least, fiscal adjustments may affect the
economic activity and vice versa. Countries are more likely to consider implementing
fiscal adjustment to reduce the debt-to-GDP ratio when they are experiencing relatively
favorable economic growth. Therefore, expansionary fiscal adjustments can be the result of
self-selection and the decision to implement a fiscal adjustment is endogenous.8 Moreover,
as many theoretical studies argue, if wealth effects and expectations are the main
channels by which the fiscal adjustments affect economic activity, the episodes identified
by the narrative approach based upon announced plans for deficit cuts can capture the
fiscal adjustments and their effects better and more correctly than those identified by
the CAPB based on actual fiscal outcomes. The main upshot of the preceding discussion is
that while the narrative approach seems superior in identifying fiscal adjustment
correctly,9 using the CAPB has the advantage in its simple and easy application.
Therefore, if the construction of the CAPB could be improved to reflect the problems
pointed out by the narrative approach, the CAPB could be a useful indicator of fiscal
policy. That is what we set out to do in the remainder of the paper.

<hs>  Data</hs>
  ~~~~

We use an unbalanced panel of OECD countries covering the period from 1970 to 2009. All
fiscal and macroeconomic data are obtained from the OECD Economic Outlook No.88.10 The
sample includes 20 countries for which we have data for 20 years or more: Australia,
Austria, Belgium, Canada, Denmark, Finland, France, Germany, Ireland, Italy, Japan, Korea,
Netherlands, New Zealand, Norway, Portugal, Spain, Sweden, United Kingdom, and United
States. To identify the instances of discretionary fiscal adjustment, we use cyclically
adjusted primary fiscal variables. In particular, we use primary fiscal variables which
exclude interest payments because the fluctuations in interest payments cannot be regarded
as discretionary. To make the cyclical correction, we follow the method proposed by
Blanchard (1993) and used also by Alesina and Perotti (1995, 1997) and Alesina and Ardagna
(1998, 2010, 2012). It is simpler and more transparent than the more complicated official
measures such as those of the OECD and IMF which utilize estimates of potential output and
fiscal multipliers (Alesina and Ardagna, 1998, 2010). The basic principle of this method
is that since the government spending depends negatively on GDP due to unemployment
benefits and the revenues respond positively to GDP due to tax receipts, the changes in
the cyclically adjusted fiscal variables can be calculated from the difference between the
predicted current-year value (which would prevail if unemployment had not changed since
the previous year) and the actual value in the previous year.11 The CAPB, however, can
also be affected crucially by changes in asset prices. For example, a stock market boom
can increase the cyclically-adjusted tax revenues because of capital gains taxes as well
as increased tax receipts due to higher private consumption and investment. As identified
by Guajardo et al. (2014), such measurement error, i.e., the correlation between the
change in the CAPB and the error term (in the regression capturing the effect of fiscal
policy on economic activity) is likely to be positive, and this could downplay the
contractionary effects of fiscal consolidation in using the CAPB. Among other studies that
highlight the importance of asset price changes to fiscal policy outcomes, Morris and
Schuknecht (2007) find that stocks and real estate wealth, which account for a significant
share of household and corporate wealth and whose value can change considerably over a
relatively short period of time, are particularly relevant for tax receipts.12 Tagkalakis
(2011a, 2011b) also finds that financial markets have a significant impact on the fiscal
positions and suggests that higher asset prices improve fiscal balances and contribute to
initiating a successful fiscal adjustment.13 Therefore, we use a share price index as an
additional variable determining the CAPB.14 The impact on fiscal balance, especially tax
revenues, can be different according to the types of asset price and tax systems (Morris
and Schuknecht, 2007; Tagkalakis, 2011a). Therefore, when considering asset price
variables as a business cycle factor, it would be ideal to include other types of asset
prices such as equities and property prices. We use only the share price index due to data
availability and its particular relevance to tax revenues. This can be deemed a limitation
of our methodology, but we believe this index is representative of the other asset price
movement.15 Guajardo et al. (2014) criticize the CAPB using the example of Ireland in
2009. In that instance, the CAPB to GDP ratio, used by Alesina and Ardagna (2010), fell
because of the decline in tax receipts due to the sharp fall in stock and house prices.
They argue that this shows the inaccuracy of the CAPB, as the Irish government was
implementing austerity reform at the time. Indeed, our new measure that takes account of
the fluctuations in asset price has the Irish CAPB improving by 1.3% of GDP in 2009.

<hs>  Definition of fiscal adjustment</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The literature identifies fiscal adjustment episodes as large and lasting changes in the
CAPB. Table 1 summarizes the definitions used in the literature: the criteria of size and
persistence are considerably different across the various studies, and even a little
arbitrary. In addition, although different studies impose different thresholds, the same
threshold is always applied to all countries. In other words, they do not allow for
country-specific heterogeneity in discretionary fiscal shocks and the private sector
responses to them. Since the expectations and confidence of the private sector are key
factors for the transmission of fiscal shocks, past fiscal record should be considered.
For example, for a country which has seldom experienced large changes in discretionary
fiscal policy, a small fiscal adjustment can send a strong signal of the government's
willingness to reduce the budget deficit. However, for a country that has had large
fluctuations of fiscal policy in the past, a similarly sized fiscal adjustment can prove
insufficient to elicit any response from the private sector. For example, while Burger and
Zagler (2008) and Guajardo et al. (2014) identify several fiscal adjustment episodes in
the U.S., Alesina and Ardagna (2010, 2012) identify none for that country. Therefore, one
should consider the idiosyncrasy of fiscal policy in each country. For this reason, we
base our definition of fiscal adjustment on the country-specific average (µi) and standard
deviations (σi) of the changes in the CAPB. Our definition for identifying fiscal
adjustment episodes has 4 criteria, incorporating size, persistence and country-specific
heterogeneity, as follows: These criteria are chosen for the following reasons. First, as
already explained, the different cut-off values reflect the heterogeneity of each
country's fiscal policy, as embodied in the average (µi) and standard deviation (σi) of
the changes in the CAPB: the standard deviation (σi) during 1970–2009 ranges from 3.73% of
GDP in Norway to 0.88% in the U.S. Second, the 3rd criterion ensures that episodes when
the CAPB improves little or deteriorates temporarily, but are offset in the following
year, are also counted. Third, the 4th criterion excludes sharp increases in the CAPB due
to one-off accounting operations such as one-time capital transfers. As in the other
studies, there is also an element of arbitrariness in our definition, in particular in
choosing the multiples (1, 1/3, 4/3, 2) of standard deviation. In the robustness section,
we use alternative rules and thresholds in order to check whether the results are
sensitive to these values. According to our definition, we identify 199 instances of
fiscal adjustment in 20 OECD countries from 1970 to 2009. These consist of 66 distinct
episodes, as summarized in Table 2 and Figs. 1 and 2.16 These episodes include only those
that led to a sufficiently large improvement in the CAPB. This list includes several well-
known episodes such as Denmark (84–86) and Ireland (82–84, 86–88). Importantly, the
episodes that are used by Guajardo et al. (2014) to illustrate the discrepancies between
the two approaches are identified correctly.17 Note that applying country-specific
thresholds for identifying fiscal adjustments need not necessarily imply that the
thresholds are generally lower. When we use Alesina and Ardagna's (2012) definition of
fiscal adjustment but account for the stock market, this results in identifying fewer
episodes for some countries but more episodes for others (results available upon request).
As Fig. 1 shows, most episodes are of short duration. Of the 66 episodes, 11 last for one
year, while 19 episodes take two or three consecutive years. The longest episode is 9
years: Japan from 1979 to 1987. Fig. 2 shows that the episodes of fiscal adjustment appear
most frequently during the 1980s and 1990s. In particular, we can observe instances of
concentrated fiscal adjustment of relatively short duration in the EU countries. This is
likely to be related to the Maastricht treaty in 1992 which set criteria for euro area
membership (Guichard et al., 2007).18

<hs>  Determinants of fiscal adjustment</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

To assess to what extent the incidence of fiscal adjustment depends on contemporaneous or
past growth as well as other macroeconomic or fiscal factors, in this subsection, we
analyze the determinants of the decision on undertaking fiscal adjustment. To this effect,
we estimate a panel logit model where the dependent variable is equal to one during
periods of fiscal adjustment and zero otherwise. Although the multi-year fiscal
adjustments can be regarded as a single episode, the fiscal authority decides not only on
initiating fiscal adjustment, but also on its continuation in the subsequent years.
Therefore, the dependent variable takes value of one for each year during an episode of
fiscal adjustment.19 Initial conditions such as the economic and policy environments can
influence the decision on fiscal adjustment. Therefore, the explanatory variables are
classified under three categories: macroeconomic, fiscal and political. The resulting
marginal effects are reported in Table 3.20 The first column contains all variables, while
the subsequent columns omit first the fiscal variables and then also the macroeconomic
ones (except contemporaneous or lagged growth).21 The result of this exercise is that
current growth is never significant unless there are no further fiscal or other
macroeconomic variables left in the regression, in which case current growth becomes
negative and significant (column 9). Lagged output gap, when included in the regressions,
is significant and negatively affects the probability of fiscal adjustment. When lagged
output gap is omitted, lagged output growth becomes significantly negative instead. As for
the coefficient of current output growth being significant in column (9), it is not clear
whether this indicates endogeneity or omitted-variable bias, given that it only appears
when no other macroeconomic or fiscal variables are present in the regression. Note also
that none of the political variables in column (9) are significant either, which suggests
that the current output growth term in effect captures only the impact of fiscal and other
macroeconomic variables. For the sake of comparison, we replicate also the analyses of
Alesina and Ardagna (2010, 2012) and Guajardo et al. (2014) with our data: these results
are not reported but are available upon request. When we do so, the current growth rate is
significant and positive when using the fiscal adjustment episodes identified by Alesina
and Ardagna (2010, 2012), and insignificant when using the fiscal adjustment episodes of
Guajardo et al. (2014). In other words, fiscal adjustments identified with the standard
CAPB-based method are more likely to occur when the growth performance is good. Our
results are thus more similar to those obtained with the narrative approach. Hence, the
episodes identified with our definition are less at risk of being endogenous than those of
Alesina and Ardagna (2010, 2012). However, since lagged output gap or lagged growth do
appear significant, the episodes identified with our definition may demonstrate less
evidence for exogeneity than the narrative episodes of Guajardo et al. (2014).22 We turn
now to the impact of our complete set of variables on the probability of fiscal
adjustment, as portrayed in column (1) of Table 3. The inflation rate has a positive
effect on the decision on fiscal adjustment, but only at the 10% significance level. The
long-term interest rate plays a significant role in prompting fiscal adjustment at the 1%
significance level: high long-term interest rate imposes greater burden on government
debt, so that it is likely to encourage fiscal adjustment. As for the fiscal variables,
the primary balance of the previous year plays a significant role. A rise in the initial
primary balance by 1% of GDP decreases the likelihood of fiscal adjustment by 2.2%. In
contrast, the initial debt-to-GDP ratio is only weakly associated with fiscal adjustment:
it is significant only at the 10% significance level and the size of the effect is very
small. Finally, most political variables turn out insignificant. Specifically, there is no
evidence supporting the ‘political budget cycle’ story, whereby the incumbent adopts
expansionary fiscal policy in an election year to stimulate the economy so as to increase
the chances of re-election. Instead, we find that the probability of adopting fiscal
adjustment does not decrease significantly in the year of general election. This may be
because our data are composed of only OECD countries with a higher level of development,
democracy and greater transparency.23 Finally, federal nations are more likely to
undertake fiscal adjustment.

<h>SPECIFICATION AND RESULTS</h>
-------------------------

With respect to the estimation, we follow the same methodology as Guajardo et al. (2014)
and Alesina and Ardagna (2012). First, we estimate equation (6) by ordinary least squares
and then compute the estimated cumulative responses of real GDP and its components to a
shock of 1% point change in the CAPB-to-GDP ratio for the first three years in order to
measure the response on the level of real economic activity variables in the log terms.25
We calculate the standard errors of the impulse response using the delta method.26 Table 4
presents the estimated coefficients of the changes in the CAPB on the economic activity
variables in our baseline model. The first column reports that growth responds negatively
to contemporaneous changes in the CAPB, but positively to its lagged change. As the
negative effect of contemporaneous fiscal adjustment is much larger than the lagged
positive effect,27 the fiscal adjustment is found to have contractionary effect in the
short term. In other words, non-Keynesian effects, or expansionary fiscal adjustments, do
not occur. In that, our results are very similar to those of Guajardo et al. (2014) based
on the narrative approach. The response of growth is mirrored in those of the individual
components of GDP. The effects of current and lagged fiscal adjustment on private
consumption and investment are very much in line with those on growth (columns 2 and 3).
As for the labor market, the effect on the real wage is negative but insignificant. On the
other hand, the effect on unemployment rate is large and positive at the 1% significance
level, both contemporaneously and with a lag. This shows that fiscal adjustment reduces
output and raises unemployment in the short term. Columns (6) and (7) show the impacts of
fiscal adjustment on interest rates. Interest rates fall when a country's fiscal position
improves, which is consistent with the finding of Ardagna (2009). Table 5 shows the
corresponding impulse-responses resulting from an improvement in the CAPB by 1% of GDP for
three years following fiscal adjustment, based on the results in Table 4. The growth rates
are cumulated to obtain the estimated impact of fiscal adjustment on the level of economic
activity, following Guajardo et al. (2014) and Alesina and Ardagna (2012). Fiscal
adjustment has statistically significant effects on GDP, private consumption and other
macroeconomic variables with the peak contractionary effect occurring within 1 or 2 years.
In particular, a fiscal adjustment equal to 1% of GDP reduces real GDP by about 0.3% in
the year of fiscal adjustment. These results are very similar to those of Guajardo et al.
(2014), despite the different definition of fiscal adjustments, specification and data.
Fig. 3 compares the responses of GDP to a fiscal adjustment shock between our baseline and
Guajardo et al.'s (2014) baseline. Although the timing of peak contractionary effects is
different, both sets of results report negative effects on GDP sustained for three years
and diminishing gradually over time.28 In summary, our results suggest that fiscal
consolidations have a significant contractionary effect in the short term. In addition,
although Guajardo et al. (2014) raise some issues with respect to using the CAPB, our own
CAPB-based measure, which takes account of those criticisms, shows results which are very
similar to theirs.

<h>ROBUSTNESS CHECKS</h>
-----------------

Next, we present the results of several alternative approaches to test the robustness of
our results. First, given that both our definition for computing the CAPB and the criteria
for identifying fiscal adjustment have an element of arbitrariness in them, we consider
alternative definitions. Second, as discretionary fiscal policy cannot be entirely
exogenous to the state of the economy, we address the issue of endogeneity in our model.
Third, we investigate the role played by the composition of fiscal adjustment in terms of
tax increases and spending cuts. Fourth, we check the robustness of our findings to the
inclusion of other variables to control for monetary and exchange rate policies, as well
as the institutional and political environment. Finally, we also investigate the
sensitivity of our results across country groups.

<hs>  Alternative definitions of fiscal adjustment</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our CAPB measure and the resulting definition of fiscal adjustment are different from the
extant literature using the CAPB approach. In particular, the thresholds applied are
arbitrary to some extent. Therefore, we perform additional analysis to assess whether
changes in the threshold affect critically the results. First, we use alternative
thresholds with respect to the standard deviation of CAPB changes. Second, since the
average and standard deviation of the changes in the CAPB for each country can be affected
by outliers, we drop the largest positive and negative values representing the changes in
the CAPB. Third, we replace the share price index with the house price index.29 Fourth, we
use the CAPB reported by the OECD instead of computing it ourselves.30 Finally, it may be
argued that the assumption of unemployment proxying business-cycle fluctuations is a
strong one. Therefore, we replace it with the output gap.31 Tables 6 and 7 show that the
baseline results (column 1) are robust to a series of alternative criteria for the
definition of fiscal adjustment and also to alternative CAPB definitions. In particular,
in column (2), we apply a lower threshold for identifying fiscal adjustment while columns
(3) and (4) apply stricter thresholds. In each case, fiscal adjustment has a similarly
sized negative effect on growth. Dropping the outliers (column 5) similarly does not lead
to substantially different results. The results obtained when the house price index is
used instead of stock prices (column 6) are not much different from the baseline either.
The results with the OECD CAPB data show an insignificant negative effect (column 7). This
difference is likely to be due to the different assumptions and methodology. As Alesina
and Perotti (1995) and Alesina and Ardagna (1998) point out, the OECD method depends on
measures of potential output, which are regarded as highly arbitrary, and a set of
elasticities of taxes and expenditures.32 In addition, although the OECD purports to
eliminate one-off transactions from the primary fiscal balance, this adjustment may not be
perfect because one-off transactions in its methodology are derived from the deviation
from trend in net capital transfers, not from individual records. For instance, the
Netherlands in 1996 is one of the cases that historical records indicate as having a one-
off transaction in the previous year, but is included in the fiscal adjustment episodes
according to the OECD CAPB version.33 Given the methodological differences, we feel that
the fact that we obtain different results with the OECD CAPB figures actually strengthens
our case. Next, we replace unemployment with output gap as a proxy for business cycle
fluctuations. In column (8), we use the output gap instead of unemployment both for
government revenue and spending, while in column (9), we use unemployment for spending and
output gap for revenue. The results are again broadly in line with the baseline.34 Table 7
compares the impulse-responses based on the estimation results. The stricter the
thresholds, the more negative the effect of fiscal adjustment on GDP. When dropping
outliers, the negative effects are smaller than in the baseline, but are still
significant. While the response in case of OECD CAPB is not significant, most estimates
indicate a decline of GDP similar to the baseline result for three years. Using output gap
instead of unemployment as a proxy for business-cycle fluctuations results in a stronger
(more negative) output response, especially when we use the output gap for both government
revenue and spending. Finally, in the preceding results, we used a single time trend for
the whole period, 1970–2009. Alesina and Ardagna (1998), in contrast, use two time trends:
1960–1975 and 1976–1994. While we do not have enough data to estimate a separate trend for
the 1970s (to account for the oil-price shocks that took place during that decade, which
was the motivation for the two time trends employed by Alesina and Ardagna, 1998), we re-
estimated our results with two time trends based on the adoption of the Maastricht Treaty
in 1992: 1970–91 and 1992–09. The impact of this change is minimal and the results are
very similar to those obtained with a single time trend (not reported but available upon
request).

<hs>  Endogeneity of fiscal adjustment</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Second, we estimate the effects of fiscal adjustment on growth under the assumption that
the decisions on fiscal adjustment and its size are endogenous to the state of the
economy. This means that since the cyclical correction cannot remove the automatic changes
of fiscal variables in response to output entirely, some of the discretionary fiscal
changes are related to the fluctuations of contemporaneous output. As a result, the fiscal
adjustment variable (ΔFAi,t-j) can be correlated with the contemporaneous error term
(νi,t): E(νi,t |ΔFAi,t-j) ≠ 0. Therefore, similar to Hernández de Cos and Moral-Benito
(2011), who also take the endogeneity into consideration, we estimate the effect of fiscal
adjustment via two-stage least squares (2SLS).35 We select the fiscal adjustments based on
the narrative approach by Guajardo et al. (2014) as the first instrument because it is
more likely to be exogenous given that the identification is based on historical records.
In addition, we use lagged long-term interest rate which we showed to be strongly
correlated with fiscal adjustment in the logit analysis of section 4 and is predetermined
but not strictly exogenous to the contemporaneous error term. The results are reported in
Tables 8 and 9 . First, when including the changes in the CAPB during normal periods, the
magnitude of the coefficient of fiscal adjustment (Table 8) and the response of GDP to a
fiscal adjustment shock (Table 9) are somewhat larger than in the baseline model, but
otherwise the results change little: we still observe contractionary effects which are
very similar to the baseline. Importantly, the changes in the CAPB that are not associated
with fiscal adjustment (NFA) do not have any effect on growth, as expected. This means
that the assumption of fiscal adjustment being different from other changes in the CAPB in
normal periods is reasonable. Next, when using instrumental variables to control for
potential endogeneity of fiscal adjustment, the effect on growth is stronger (more
negative) than in the baseline. This pattern appears regardless of the instruments used.
Table 10 reports the results of first stage regressions, confirming the validity of the
instruments considered. Both instruments have strong relation with fiscal adjustment.
However, the test results indicate that the narrative fiscal adjustment of Guajardo et al.
(2014) has more explanatory power than the lagged long-term interest rate. When we use
both instruments at the same time, the results are also rather similar to those obtained
with each instrument alone. In addition, according to the Durbin–Wu–Hausman test for
endogeneity of fiscal adjustment, the null hypothesis that the fiscal adjustment can be
treated as exogenous is rejected at the 5% significance level. Therefore, we can conclude
that fiscal adjustment identified by the changes in the CAPB is not strictly exogenous to
growth. Nevertheless, the results corrected for endogeneity of fiscal adjustment support
our baseline finding of contractionary effects.

<hs>  Does composition of fiscal adjustment matter?</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Many studies analyze whether the effects of fiscal adjustment depends on its composition.
They generally agree that fiscal adjustments focusing on the spending side are more likely
to have expansionary effects on GDP than those on the tax side. Therefore, in this
subsection, we investigate what role the composition of fiscal adjustment plays in the
response of economic growth. First, we divide the fiscal adjustments episodes into two
types: ‘spending-based’, in which the change in the CAPB is mainly (by at least 50%) due
to spending cuts, and ‘tax-based’, in which the change in the CAPB is mainly due to
revenue increases (Guajardo et al., 2014 and McDermott and Wescott, 1996, apply the same
criterion). Next, we implement another categorization of fiscal adjustments, splitting
them into three types: ‘pure spending-based’ ones where the improvement in the CAPB is
entirely due to spending cuts, ‘pure tax-based’ ones which are totally due to revenue
increases, and ‘mixed’ cases that combine the two types of adjustment. Fig. 4 shows the
estimated effects of fiscal adjustment according to its composition. First, although
spending-based adjustments do not have a significant expansionary effect, they also do not
have significantly negative effect on GDP and private consumption except in the year of
fiscal adjustment. When compared with tax-based adjustments, spending-based adjustments
are less contractionary and can even offset the large negative effects of tax-based
adjustment because the response of the baseline is in between the responses associated
with the two types of fiscal adjustment. This result is consistent with Alesina and
Ardagna (2012). On the other hand, tax-based fiscal adjustments have a contractionary and
statistically significant effect on GDP with a peak negative effect of −0.68% and on
private consumption with a peak negative effect of −0.71% within three years. When the
composition of fiscal adjustment is classified into three types, as shown in column (2) of
Fig. 4, the results do not differ much. While the results for mixed adjustments are almost
the same as the baseline, pure tax-based fiscal adjustments decrease GDP significantly
whereas pure spending-based fiscal adjustments appear contractionary but the effect is not
statistically significant even in the year of fiscal adjustment. An alternative way is to
identify fiscal adjustments based on large changes of fiscal variables rather than by
looking at changes of fiscal balance: as an increase in cyclically-adjusted revenues or a
decrease in cyclically-adjusted spending. Although this method is different from the
conventional method based on fiscal balance, it has several advantages. First, we can
capture some episodes of fiscal adjustment which might be otherwise excluded. This is the
case when the fiscal adjustment on spending (revenue) side is offset by a counter-
balancing change of revenue (spending). Second, we can reduce the risk that the results
are driven by a particular threshold (e.g. 50%) chosen to identify tax-based and spending-
based adjustments. Therefore, we re-identify fiscal adjustments based on large changes of
cyclically-adjusted revenues and spending respectively.36 The former are denoted as ‘tax
side’ and the latter denoted as ‘spending side’. Then, we replace ΔFA in the baseline
specification with these two types of fiscal adjustments to estimate their effects on GDP
and private consumption. Fig. 5 shows the estimated effects of fiscal adjustment according
to its composition. While fiscal adjustments based on an increase in revenues have a
largely contractionary and statistically significant effect on GDP and private
consumption, fiscal adjustments based on a decrease in spending have a small expansionary
but not statistically significant effect on GDP and negligible effects on private
consumption. Therefore, we still cannot find any firm evidence of expansionary effects
even in the case of fiscal adjustment based on large spending-cuts. However, this
reconfirms that spending-based adjustments are less contractionary than tax-based ones,
which is consistent with the previous results of compositions of fiscal adjustment based
on the CAPB. Guajardo et al. (2014) argue that a possible reason for the different effects
depending on the compositions of fiscal adjustment is that monetary policy is more
favorable in case of spending cuts. They suggest that central banks conduct monetary
stimulus more actively following spending cuts than after tax hikes so that the policy
rate increases in response to tax hikes and decreases in response to spending cuts.37
Therefore, we investigate the response of short-term interest rate to the two types of
fiscal adjustment. As Fig. 6 shows, the response of the short-term interest rate is
significantly different according to the two types of fiscal adjustment only in the year
of fiscal adjustment. After one year, the short term interest rate falls significantly in
both cases. Therefore, this result can partially support the argument of Guajardo et al.
(2014) that the different effects depending on the composition of fiscal adjustment are
ascribed to different monetary policy stances.

<hs>  The role of the economic environment</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Next, we check the robustness of our findings by including the short-term interest rate
and the real effective exchange rate among the regressors.38 These two additional control
variables are aimed at accounting for monetary policy and exchange rate policy
respectively. Table 11 and Fig. 7 show the results. The fit of the regression improves
when we include variables relating to the economic policy. The coefficient of fiscal
adjustment, as well as that for tax-based adjustment, remains significantly negative,
although they are smaller than those without controlling for policy variables. Similarly,
spending-based fiscal adjustment has a smaller negative coefficient, but is still
statistically insignificant. The change of effects can be attributed to monetary policy in
that the short-term interest rate has a significantly negative effect on growth, as
expected, but the exchange rate is not significant. Fig. 7 confirms that fiscal
adjustments have less contractionary effect on GDP when we control for monetary policy
than in the baseline. Therefore, monetary policy can affect the response of GDP to fiscal
adjustment shocks. If the short-term interest rate falls, it leads to an increase in GDP.
Therefore, if fiscal adjustment coincides with a large reduction in the short-term
interest rate, this may stimulate the economy in the following periods. However, even in
this case, this result is to be attributed not to the fiscal adjustment, but to the lax
monetary policy. In regard to the effects of composition of fiscal adjustment, Fig. 7
shows that the response of GDP is larger in tax-based fiscal adjustments than in spending-
based ones. Therefore, as Fig. 6 in the previous subsection shows, if the discretionary
monetary policy responds differently according to the type of fiscal adjustment, this
could help account for the different effects depending on the composition of fiscal
adjustment. However, it cannot be a decisive factor, contrary to the argument of Guajardo
et al. (2014), in that when we control for the short-term interest rate, there is still a
large difference between the effects of tax-based and spending-based fiscal adjustment on
GDP. Furthermore, there can be other omitted factors that are likely to influence the
effects of fiscal adjustment on economic activity. The omission of relevant variables
could bias the response of output in estimating the effects of fiscal adjustments.
Therefore, we add additional variables into the baseline model one by one. The initial
government debt is considered because a high debt level can lead to expansionary fiscal
adjustment via the wealth effect. International factors such as the exchange rate regime
and financial openness can be taken into account as another potential factor. Furthermore,
Ilzetzki et al. (2011) find that the degrees of exchange rate flexibility and openness to
current and capital account transactions are critical determinants of the size of fiscal
multiplier. Therefore, we include the exchange rate regime and financial openness index.39
We also include dummies for Euro Area membership and for participation in IMF programs.
Political environment can similarly play a role and therefore we include a dummy for
countries with a federal system of government and a measure of ruling party ideology (the
latter is obtained from Potrafke, 2009). Finally, we also include lagged inflation and the
long-term interest rate as two potentially important macroeconomic variables. Tables 12
and 13 show the regression results obtained when we control for the impact of these
additional factors. The results are very similar to the baseline results, as is clear from
column (10) of Table 12, where all the variables are included in the same regression. Here
GDP growth (T-1), ΔFA (T) and ΔFA (T-1) remain highly significant, as in the baseline, and
the signs as well as magnitudes of their coefficients remain remarkably similar. Moreover,
all of the additional controls turn out insignificant in column (10), with the exception
of gross debt, inflation and long-term interest rates, all of which have a negative effect
on growth, which is intuitive. As regards columns (1)–(9), where one variable at a time is
added to the baseline, we find that only the exchange rate regime and the long-term
interest rate are significant. Aside from the fairly comprehensive list of variables
considered, regulatory reform such as labor and product market institutions, and
structural reforms should be considered as significant and relevant factors influencing
the estimated effects of fiscal adjustment on economic activity. Several studies
investigate the interactions between fiscal adjustment and these market institutions and
structural reforms and show that these regulatory policies can play a significant role in
initiating fiscal adjustment and determining its success (Guichard et al., 2007;
Hauptmeier et al., 2006; Tagkalakis, 2009).40 However, when these are controlled for, the
qualitative effects on economic activity of fiscal adjustment does not change (Alesina and
Ardagna, 2012; Hernández de Cos and Moral-Benito, 2011). Although we do not address the
effects of labor and product market institutions and structural reforms during the fiscal
adjustment episode in this paper, they can affect the responses of output to fiscal
adjustment in the long term as well as quantitatively via employment and investment
behavior.

<hs>  Effects of fiscal adjustment across country groups</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The effects of fiscal adjustment on the economic activity may be different according to
the sensitivity of private agents, which in turn depend on the past trajectory of fiscal
policy. While our definition of fiscal adjustment controls for country-specific
heterogeneity, in this subsection, we explore this issue further by dividing the 20
countries into two groups on the basis of two criteria: the frequency of fiscal
adjustments and the volatility of discretionary fiscal policy. For the first criterion,
high and low frequency groups include 10 countries each. Similarly, high and low
fluctuation groups each consist of 10 countries according to the standard deviation of
changes in the CAPB.41 Table 14 reports the estimated responses of GDP and private
consumption to a fiscal adjustment shock. Interestingly, for the high group in terms of
both frequency and fluctuation, economic activity displays a significantly negative
response only in the year of fiscal adjustment. On the other hand, the low groups in
frequency and fluctuation alike display a strong response to fiscal adjustment in all
years. This finding supports the notion that economic agents respond more sensitively to
unexpected or unusual shocks. When fiscal policy undergoes frequent changes, agents become
accustomed to such changes and their responses become smaller.

<h>CONCLUSIONS</h>
-----------

This paper investigates the short-term macroeconomic effects of fiscal adjustment in 20
OECD countries over the period 1970–2009. This issue has been studied in many previous
contributions already. Recently, it has become more central in academic and policy circles
due to the rising fiscal deficits and public debts during the current global crisis. Much
of the literature argues that fiscal adjustments can promote economic output even in the
short term. However, after identifying fiscal adjustment episodes from historical
documents, Guajardo et al. (2014) conclude that fiscal adjustments are always
contractionary. They also criticize the CAPB-based measures used in the rest of literature
as being imprecise and biased toward overstating the potential expansionary effects of
fiscal adjustments. This paper reconsiders the CAPB-based measure in order to identify the
fiscal adjustment episodes more accurately, taking into account the problems identified by
Guajardo et al. (2014). The main features of our new measure of fiscal adjustment are as
follows. First, we consider the effect of asset price fluctuations on tax revenues when
cyclically correcting the fiscal balance. Second, our criteria for selecting fiscal
adjustment episodes allow for the heterogeneity of individual countries in fiscal policy,
contrary to the uniform approach in the previous literature. Third, our criteria account
for temporary one-off transactions and temporary adverse shocks which can undermine the
accuracy of the CAPB. Although Guajardo et al. (2014) argue that the CAPB is an unreliable
guide regarding fiscal adjustment, our new criteria identify fiscal adjustment episodes
that largely overlap with their narrative-based ones. Based on the fiscal adjustments
identified, we estimate the effects of fiscal adjustment on economic activity. Our key
result is that a fiscal adjustment has contractionary effects on economic activity in the
short term. This provides little support for the expansionary fiscal adjustment
hypothesis: such ‘non-Keynesian effects’ are very limited and probably occur only under
specific conditions, not generally. This is consistent with the results of Guajardo et al.
(2014). As for the role of the composition of fiscal adjustment, spending-based fiscal
adjustments lead to smaller reductions of output than tax-based fiscal adjustments. This
finding is in line with most of the literature regardless of the approach used. Further
work could explore in more depth the effects of fiscal adjustments. First, as for the
reasons behind the different effects of tax-based and spending-based adjustments, more
detailed disaggregation of fiscal spending and taxes could be used for the analysis.
Second, most of the literature on fiscal policy has studied developed countries such as
the OECD because of data limitations. However, as the data for developing countries have
become more easily available lately, the fiscal adjustment in developing countries also
needs to be investigated for the comparison with developed countries' results. Another
possible extension would address the anticipation effects by private agents through
comparing the narrative data based on announced plans with the CAPB-based data based on
actual outcomes. However, to capture the timing of fiscal adjustment accurately, quarterly
rather than annual data may be required.


<h>REFERENCES</h>
----------

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<ART>Market Potential and Global Growth over the Long Twentieth Century
==================================================================

Authors: David S. Jacks, Dennis Novy
DOI: 10.1016/j.jinteco.2018.07.003
Year: 2018  |  Pages: 221-237
ASJC codes: 2002, 2003
Keywords: Economic geography, Market potential, Structural gravity, Trade costs

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We examine the evolution of market potential and its role in driving economic growth over the long twentieth century. Theoretically, we exploit a structural gravity model to derive a closed-form solution for a widely-used measure of market potential. We are thus able to express market potential as a function of directly observable and easily estimated variables. Empirically, we collect a large dataset on aggregate and bilateral trade flows as well as output for 51 countries. We find that market potential exhibits an upward trend across all regions of the world from the early 1930s and that this trend significantly deviates from the evolution of world GDP. Finally, using exogenous variation in trade-related distances to world markets, we demonstrate a significant causal role of market potential in driving global income growth over this period.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

What has been the trajectory of market potential over the long twentieth century? And is
there a causal relationship between market potential and global income growth? Here, we
contribute to a long-standing literature along these lines by developing a structural
measure of market potential which is fully comparable across countries and across time and
which comes with fairly minimal data requirements. As in the preceding literature, we
model market potential as a summary measure of both external and internal demand which
explicitly takes into account the costs of transaction and transport associated with the
exchange of goods. But in contrast to much of the preceding literature, we seek to exploit
the wide variation in the evolution of the global economy over the long twentieth century
to investigate the causal role of market potential in shaping global income growth over
this period. Our goal, then, comes in assessing the relationship between globalization and
growth in the long run by: (1) developing a theoretically- derived measure of market
potential appropriate for historical use rather than relying on narratives derived from
“data-as-given” time series such as aggregate exports, allowing us to relate globalization
and growth in a more disciplined fashion; (2) collecting a new dataset on aggregate
exports, bilateral trade, and GDP for 51 countries; (3) constructing our proposed measure
of “structural market potential”, as well as charting and decomposing its evolution
through time; and (4) exploiting exogenous variation in trade-related distances to world
markets in order to determine the causal role of market potential in driving global income
growth over this period. Of course, we are far from the first to consider the theme of
market potential and its role in the growth process. In the very first contribution to
this literature, Harris (1954) was motivated by the question of why, with only 12% of the
United States by area, the Northeast produced fully 50% of its manufacturing output and
employed 70% of its industrial labor force in 1950. His informal model is one in which
firms balance production versus trade costs in determining their location and in which the
presence of deep input and output markets influence this decision. His paper also marks
the first usage of the term market potential which Harris defines as “an abstract index of
intensity of possible contact with markets” and is calculated as the sum of markets
accessible (often proxied by income or population) to a given point over distance-to-
markets from that point. Krugman (1991, 1992) resurrected this notion of market potential
but explicitly grounded it in a spatial general equilibrium model, thereby setting off an
expansive body of work in the new economic geography literature. The basic structure of
the Krugman model was then extended by Helpman (1998), enhancing its tractability in
empirical work (e.g., Hanson 2005). In addition, Fujita et al. (1999) gave rise to the
workhorse model of the new economic geography literature. Importantly, these modeling
approaches rely on a common set of elements, typically in the form of CES consumption,
simple production functions and monopolistically competitive firms. Symmetry in
preferences and technology yield a structural link between market potential and standards
of living. For our purposes, however, the most important contribution to this literature
comes from Redding and Venables (2004). Motivated by the wide dispersion in cross-country
manufacturing wages and incomes, they concentrate on two mechanisms which may potentially
explain such disparities: (1) the distance of countries to markets in which their output
is sold; and (2) the distance of countries to markets from which capital and intermediate
goods are purchased. Thus, the presence of trade costs means that more distant countries
face a penalty on their sales as well as additional costs on imported inputs. As a
consequence, firms in these countries can only afford to pay relatively low wages,
translating into lower levels of GDP per capita. This result holds even if technologies
are the same across countries. Liu and Meissner (2015) recently considered the theme of
historical market potential in the context of the Redding and Venables (2004) model. Using
cross-sectional data for 27 countries in 1900 and 1910, they establish that market
potential was a significant determinant of GDP per capita in the early twentieth century.
They also raise the prospect that the United States did not necessarily benefit from a
natural lead in market potential as its greater domestic market size was counterbalanced
by its greater distance to other—in particular, European—markets. Finally, Head and Mayer
(2011) consider panel evidence for the role of market potential in driving differences in
GDP per capita for the period from 1965 to 2003. Thus, they are able to establish a
broader consistency with the results of Redding and Venables (2004). However, we argue
that there is a complication with Redding and Venables' approach in a panel setting, which
makes its use in a historical context potentially problematic. Namely, one ideally needs a
full matrix of bilateral trade flows for every year, imposing a large cost in terms of
data collection. This is due to the fact that the construction of market potential in
Redding and Venables (2004) and Head and Mayer (2011) relies on a set of exporter and
imported fixed effects pertaining to all countries in the world, based on a standard
gravity model of bilateral trade. Without the full matrix of global trade flows, estimates
of these fixed effects can shift substantially.1 Our proposed solution, then, comes from
exploiting a link between the model of Redding and Venables and structural gravity models
that allows us to bypass exporter and importer fixed effects. The rest of the paper
proceeds as follows. Section 2 lays out the relationship between market potential and
structural gravity. It does so first by revisiting the work of Redding and Venables (2004)
on market potential and then by relating it to the work of Anderson and van Wincoop
(2003). This results in a new solution for the measure of market potential that is less
data-intensive and therefore particularly suitable for historical settings. We refer to it
variously as “structural market potential” or, simply, market potential. Section 3
introduces the underlying data, presents our new evidence on market potential over the
long twentieth century, and provides a comparison to existing formulations of market
potential. Section 4 first relates our new measure to global growth in the context of
standard wage equations drawn from the existing literature and then exploits variation in
trade-related distances to world markets in order to establish a causal relationship
between market potential and global income growth. Finally, Section 5 concludes.

<h>MARKET POTENTIAL AND STRUCTURAL GRAVITY</h>
---------------------------------------

We first outline the basic setup of the Redding and Venables (2004) new economic geography
model. We then relate it to the structural gravity framework by Anderson and van Wincoop
(2003). As a departure from the existing literature, this allows us to derive an
analytical solution for the market potential measure mainly in terms of directly
observable and easily estimated variables.

<hs>  The new economic geography model</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Apart from the demand-side aspect captured by market capacity, the right-hand side of eq.
(2) also contains supply-side variables in the form of nipi1−σ, net of bilateral trade
costs tij. Redding and Venables (2004) refer to this term as the supply capacity of
country i, si ≡ nipi1−σ. It consists of an extensive margin measure ni for the number
products originating in i as well as their price competitiveness embodied by pi. Redding
and Venables (2004) provide further details for the supply side of the model. For
instance, they impose a Cobb-Douglas technology with an immobile factor (e.g., labor), an
internationally mobile factor (e.g., capital), and a composite intermediate good with
price Pi. They introduce increasing returns by way of a fixed input requirement.3 It turns
out, however, that the supply-side details are not essential for the aggregate gravity
relationship that emerges from the model as the basis for the empirical analysis.4

<hs>  Exploiting the link with structural gravity</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

All else being equal, MAi increases in global income. Intuitively, if the global economy
grows, demand for individual country i's output rises. In contrast, SAi decreases since
the growth of production in the world represents more competition and thus a decline in
relative supply capacity. Not surprisingly, growing yi increases both market and supplier
access since it represents both rising availability of supply to customers elsewhere as
well as rising demand for foreign products. Higher domestic trade costs tii work in the
opposite direction since they hamper the domestic economy. We can think of tii as the cost
of reaching domestic customers and sourcing domestic supply. The role of domestic trade
flows xii is perhaps less obvious to understand. Holding output constant, due to market-
clearing a rise in xii means less trade with foreign countries, which implies that
bilateral trade costs tij must have risen. A rise in bilateral trade costs is associated
with more isolation from global markets, which in turn hurts demand prospects as well the
ability to obtain the supply of goods emerging from partner countries. We draw two
conclusions for our empirical analysis. First, since the market and supplier access
measures are proportional, for a given cross-section they do not contain independent
information. Therefore, we proceed with a single measure corresponding to the expression
for market access in (12). We variously call it “structural market potential”, or, simply,
market potential (MPi). Second, in contrast to the previous literature, we do not
necessarily require estimates of or information on bilateral trade costs across countries
to compute our market potential expression (12). Instead, it is a simple function of
variables related to the domestic economy and a global constant.9 Moreover, the variables
in eq. (12) are for the most part given by the data. That is, income yi as well as global
income yW are directly observable while domestic trade flows xii can be constructed from
the data. Domestic trade costs scaled by the elasticity of substitution, tiiσ−1, can be
constructed based on estimates from a standard gravity regression using domestic trade
cost proxies such as internal distance as we do here (details below).

<hs>  The dataset</hs>
  ~~~~~~~~~~~

We collected a large annual dataset for 33 countries over the period from 1910 to 2010
which is comprised of aggregate exports and GDP and for an additional 18 countries from
1950 to 2010. We chose to begin data collection in 1910 in order to maximize the cross-
section of countries at our disposal. This data includes newly collected trade
observations, in particular, for the periods spanning the World Wars. We provide details
on our sources in Appendix III while Fig. 1 summarizes the sample graphically. Countries
in black (n = 33) are those for which the full complement of output and trade data is
available from 1910 while those in grey (n = 18) are those for which consistent data is
available only from 1950. The sample countries represent roughly 75% of world GDP in 1910,
roughly 85% of world GDP in 1950, and roughly 90% of world GDP in 2010.

<hs>  Constructing market potential</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We construct our preferred measure of market potential as given in eq. (12). This approach
does not require estimation of the entire term as we simply insert the data directly into
the right-hand side expression. Thus, the data on income yi and global income yW are
readily available. We construct domestic trade as the difference between income and total
exports, xii = yi – xi, where xi denotes total exports. As income is measured as GDP and
is cast in value-added terms, it is in principle not consistent with exports as a gross-
value measure. However, as a robustness check, we are able to use total gross
manufacturing production instead of GDP for the years from 1980 to 2006. This leaves our
main results materially the same, a point we discuss in fuller detail in Appendix II.11 As
a caveat, we stress that a shortcoming of the measure for tii is that a number of
components that arguably matter for domestic trade costs, such as domestic infrastructure,
are left out. Given that the distance and contiguity measures do not change over time, the
changes in domestic trade costs are driven by time-varying gravity coefficients. It would
be preferable to have a more detailed, country-specific time-varying measure of domestic
trade costs, but limited data availability poses restrictions in that regard. Measuring
domestic trade costs is an active area of research (e.g., Ramondo et al. 2016), and better
measures might improve market potential measures such as ours in the future. Fig. 2a shows
the average of the log values of market potential for two samples, indexed to a value of
100 in 1950. The first sample is comprised of all 33 countries for which we have a
complete set of aggregate export and GDP data from 1910. The second sample is comprised of
the same plus the 18 countries for which we have a complete set of aggregate export and
GDP data from 1950. While Fig. 1 might suggest that there may be non-random sample
selection across the start dates of 1910 and 1950, Fig. 2a indicates this is likely a non-
issue as the correlation between the two series is in excess of 0.99. In general, there is
a clear upward trend driven by the growth of the world economy, with periods of global
depression and recession in the early 1930s, the early 1980s, the early 1990s, and the
late 2000s registering as troughs in the series. Underlying these global patterns is
substantial heterogeneity with large and persistent—albeit unreported—differences in the
levels of market potential across continents, e.g., Latin versus North America or Asia
versus Europe. At the same time, Fig. 2a plots the log value of world GDP, also indexed to
a value of 100 in 1950. We do so to assuage concerns that our measure of market potential
captures nothing more than the evolution of world economic activity over the long
twentieth century. For sure, the various series for market potential and world income
exhibit a somewhat similar upward trajectory, but it is clear from Fig. 2a that there is
very little variation in world income growth from year to year. In contrast, our measures
of market potential register significant divergence from world income. And it is precisely
this variation which we will use below to identify the causal effect of market potential
on economic growth at the individual country level. Based on eq. (14), we can also extract
and plot the implied price index Pi by removing world income from the market potential
measure. Here, we assume a value for the elasticity of substitution of σ = 5. In Fig. 2b,
we plot this implied price index for two key economies, India and the United Kingdom,
normalized to 100 in the year 1910. How should we interpret this implied price index?
Consider the following benchmark case. If trade costs did not change and the world
experienced uniform income growth across all countries, then the price indices would not
change.14 In that case, market potential would follow exactly the same trend as global
income over time. By contrast, higher trade cost levels serve to increase these price
indices. This is precisely what we observe from 1910 to 1930, reflecting rising
protectionism in the interwar period. More specifically, the price index rose by 92% for
India and 70% for the United Kingdom. This rise is then followed by falling price indices,
reflecting a long-run trend of declining trade barriers and increasingly open economies.
Overall, the implied price indices can be interpreted as an inverse proxy of our
“structural market potential” measure. We stress that these price indices are not the same
as conventional consumer price indices (and therefore not directly observable) since they
may also capture non-pecuniary trade frictions such as information barriers (see Anderson
and van Wincoop 2003). In this vein, we note that there is significant variation in market
potential—particularly in relative terms—across individual countries. As an example, Fig.
3 speaks to this issue by considering the trajectories of the log of market potentials for
India and the United Kingdom over the long twentieth century. There, it is apparent that
while much of the variation in the two series is shared in common—again, driven by the
evolution of world income—there is still scope for differential rates of growth in market
potential in the long run. This is seen most clearly in the ratio of the two series
(UK:IND). It rises up to 1930 when the United Kingdom's lead attains its maximum and then
consistently falls into the present day where Indian and UK market potential stand nearly
at par.15 To further our understanding of the underlying spatial correlations, we compute
Moran's I for various years. This measure takes on a value of −1 in the case of perfect
dispersion (negative spatial autocorrelation), a value of close to 0 in the case of random
spatial arrangement, and a value of +1 in the case of perfect positive spatial
correlation. We compute Moran's I for the logarithmic values of our market potential
measure for the sample from 1950 (n = 33), and also for logarithmic GDPs as a
comparison.16 We follow the common approach of giving a weight of 1 to neighbors in the
spatial weights matrix and a weight of 0 otherwise (i.e., we use the contiguity indicator
variable in the spatial weights matrix). The resulting values of Moran's I for log market
potential are 0.94, 0.94, and 0.88 for the years 1950, 1980, and 2010, respectively. The
corresponding values of Moran's I for log GDP are 0.59, 0.53, and 0.51. We make two
observations. First, market potential is more strongly spatially correlated than GDP. This
finding is intuitive given that many large economies tend to be spatially clustered, e.g.,
in Western Europe. Second, the degree of spatial correlation declines over time but only
in a minor way. This finding can be explained, for instance, by the shift of global
economic power away from Europe and North America towards Asia.

<hs>  A comparison to Redding and Venables (2004) and Harris (1954)</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The previous literature constructs market and supplier access measures (3) and (4) by
estimating eq. (8) for xij where supply capacity si and market capacity mj are taken as
exporter and importer fixed effects, respectively. Redding and Venables (2004) follow this
procedure for a single cross-section in 1994. Head and Mayer (2011) have panel data for
the period from 1965 to 2003 and estimate the fixed effects year by year. The use of
exporter and importer fixed effects implies a specific normalization due to the omitted
exporter/importer category. For instance, Redding and Venables (2004) omit the exporter
fixed effect for the United States as a normalization and also omit the constant in their
specification such that no importer fixed effect has to be dropped. In contrast, our
method of constructing market potential through eq. (12) does not directly rely on
exporter and importer fixed effect estimates and thus avoids the year-by-year
normalization. While we readily acknowledge that Redding and Venables were only concerned
with market potential across the countries of the world at a given point of time, one
benefit of our measure is that it allows us to more consistently compare levels of market
potential over time.17 Fig. 4 follows Fig. 3 by considering the trajectories of the log
values of the market access measure, MAi, for India and the United Kingdom for the period
from 1910 to 2010. As in Fig. 3, there is a fairly consistent, upward trend throughout the
second half of the twentieth century and the first decade of the 21st century. However, in
Fig. 4, we also observe two sharp increases in market access during the first half of the
twentieth century to the extent that the average (log) values for market access for the
United Kingdom in 1919 and 1946 exceed those for 2010. Taken purely at face value, this
would seem to be an implausible result given what we know about global macroeconomic
history, in particular the role of the World Wars in disrupting global trade flows (Jacks
et al. 2011). There is also the related issued that the relative value, UK:IND, is
remarkably flat, hovering around a value of 1.05 throughout the long twentieth century.
Thus, while the approach of Redding and Venables (2004) is very useful for a given cross-
section of data, our results suggest caution in blindly using it in repeated cross-
sections particularly during periods when international trade flows are heavily distorted
by global conflict. For our purposes of both charting and understanding the trajectory of
market potential over the long twentieth century, we therefore prefer the measures
presented in Figs. 2a and 3.18

<hs>  Decomposing the growth of market potential over time</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

To understand the decomposition in eq. (17), it is useful to consider the hypothetical
benchmark of income growing by the same uniform rate across all countries. In that case,
the income and domestic trade shares in the square brackets would not change, and market
potential would be driven exclusively by overall global income growth through the last
term. If one country grew faster than the otherwise uniform rate, its market potential
would rise more quickly than elsewhere. In Table 1, we present the results of
decomposition (17), constructing the right-hand side variables as described in section
3.2. We use our sample of 33 countries that we group by five regions (Asia, Australia/New
Zealand, Europe, Latin America, and North America). We present a decomposition for the
full period from 1910 to 2010 as well as separate decompositions for the periods from 1910
to 1960 and from 1960 to 2010. Overall, market potential grew by 305% across countries on
average over the full period. Perhaps not surprisingly, this growth is rather similar
across regions as global income growth serves as a common factor in driving market
potential. However, this comparison of 1910 versus 2010 heavily masks important
differences across sub-periods. In particular, countries experienced only very moderate
growth in market potential prior to 1960. This was a period marked by isolationism and war
with an associated rise in trade costs as well as domestic trade shares (see Jacks et al.
2011). In contrast, the period after 1960 was characterized by sizeable (positive)
contributions to the growth in market potential stemming from declining trade costs and
increasing openness. In particular, Asia experienced above-average growth in market
potential due to its expanding share of global income while the opposite was the case for
Europe.

<h>WAGE EQUATION REGRESSIONS</h>
-------------------------

Here, we return to one of the motivating questions for this paper, namely whether there is
a causal relationship between market potential and global income growth. In what follows,
we first establish that our new measure of “structural market potential” delivers results
from so-called wage equation regressions which are consistent with those found in Redding
and Venables (2004) and Hanson (2005) among others. However, in their work, the expression
for market access is conveniently separable into two constituent components, domestic and
foreign market access. Thus, the latter of these two strips away any domestically-
determined elements of demand. This contrasts with our measure of “structural market
potential” which will clearly be endogenous in light of the presence of domestic output in
eq. (12). In order to break this mechanical link in between income (per capita) and market
potential, we then use exogenous variation in trade-related distances to world markets as
an instrument, finding an economically and statistically significant role for market
potential in driving global income growth over the long twentieth century.

<hs>  Wage equation regressions in levels</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

An appropriate starting point is provided by Redding and Venables (2004). In their work,
they derive what is known as a wage equation, i.e., an equation that structurally relates
the price of the immobile factor of production (or wage) to a country's market
access/market potential. Based on their model, the same wage equation would arise in our
context. Redding and Venables demonstrate a strong association between GDP per capita
(their proxy for wages) and both domestic and foreign market access in the cross-section.
This association remains even after conditioning on a large number of covariates and
controlling for potential endogeneity. Head and Mayer (2011) run an analogous set of panel
regressions, finding results consistent with those of Redding and Venables. However, with
our new measure of structural market potential, it is an open question whether this
empirical regularity remains intact. Table 2 first tries to establish the simple
association between the log of GDP per capita and the log of market potential. Standard
errors are clustered on countries here—and in all regressions—to control for within-
country serial correlation of arbitrary form.19 The coefficient reported in column (1) is
precisely estimated and comparable in magnitude to that reported by both Redding and
Venables (2004) and Head and Mayer (2011). Of course, there are many other potential
determinants of GDP per capita, and the specification in column (2) thus controls for both
common patterns over time and fixed, unobserved country-level characteristics. This
estimation then relies upon variation within countries over time which is not determined
by global shocks or trends such as the evolution of world GDP over time. That the
coefficient actually increases in magnitude is a reassuring sign of our measure's
salience. The next two columns repeat the regression for different samples. The full
sample in columns (1) and (2) includes 33 countries with observations on market potential
and GDP per capita from 1910 to 2010 and 18 countries with observations on market
potential and GDP per capita from 1950 to 2010. A brief review of Fig. 1 suggests the
former are predominantly developed nations in North America and Western Europe while the
latter are mainly developing nations in Africa and Asia. Column (3), which is based on the
balanced sample dating from 1910 only, shows a point estimate which is smaller than that
in column (2) but which is still highly statistically significant. Given the countries
that join the sample in 1950 and that are part of the sample for column (2), this might
suggest that the link between market potential and GDP per capita may have become stronger
over time and/or is stronger for developing nations. Column (4) excludes observations
spanning the two World Wars, specifically the years from 1914 to 1919 and from 1939 to
1949. These observations may be problematic if these years entailed a breakdown in normal
economic relationships or suffered a deterioration in terms of data quality. The magnitude
of the elasticity between GDP per capita and market potential is virtually unaffected. In
any case, we still favor the results in column (4) as it addresses the most serious
concerns related to sample selection across countries and years and data quality. The
final two specifications average our measures of market potential and GDP per capita over
(non-overlapping) five- and ten-year periods, respectively, and represent our preferred
specifications. This approach of aggregating over time can be thought of as reducing the
role of measurement error in particular years as well as diminishing the potential role of
domestic and global business cycles in driving the results. Across columns (5) and (6),
the values of the coefficients are stable and broadly similar to column (4), again
pointing to a tight—but not necessarily causal—relationship between levels of GDP per
capita and market potential throughout the long twentieth century.

<hs>  Wage equation regressions in differences</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Table 3 follows the regressions of Table 2 but considers a different set of dependent and
independent variables. Instead of considering the logs of GDP per capita and market
potential, we follow Hanson (2005) by estimating the wage equation in log differences.
This allows us to better account for potential serial correlation in the specifications of
Table 2 and is closer in spirit to this paper's theme of economic growth and market
potential. Comparing Table 3 to Table 2 across the various specifications in columns (1)
through (6) reveals that the estimated elasticities remain statistically significant.
However, they are smaller in magnitude, suggesting a plausible role for country-level,
time-varying omitted variables in driving the earlier results. With respect to the
specifications in columns (5) and (6) in Table 3 compared to those in Table 2, the results
are more encouraging in this regard. The point estimates in Table 3 are smaller in
magnitude as before, but they are statistically indistinguishable from those in Table 2.
Honing in on our preferred specification in column (6), the results suggest that every
percent change in market potential was matched with a roughly 0.65% change in GDP per
capita. Taking this result at face value suggests that a significant share of global
growth over the long twentieth century could be attributed to changes in market potential
in the long run.

<hs>  Wage equation IV regressions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Of course, there are good reasons why these results should be approached with caution.
Above all, there is clear endogeneity in any wage equation regression given the way our
measure of market potential is constructed in eq. (12) as a function of domestic output.
Facing a similar problem, Redding and Venables (2004) as well as Head and Mayer (2011)
instrument market potential with measures of geographic centrality, namely a country's
distance from Belgium, Japan, and the United States. Naturally but unfortunately, such
measures do not vary over time, a condition which underlies many other possible
instruments for market potential. Faced with this prospect, we instead draw inspiration
from a series of papers by Feyrer (2009a, 2009b). In Feyrer (2009b), the author begins
with the observation that historically the vast majority of international trade by value
has been conducted via sea routes and that to this day the vast majority of international
trade by physical volumes continues to be conducted in this manner. However, presently, a
very large share—upwards of 40%—of international trade by value is conducted via air
routes as improvements in aircraft technology and logistics have enhanced the air
industry's importance in this regard. Thus, over time countries with shorter air routes to
its trading partners relative to its sea routes (e.g., India) have benefited more from
this exogenous technological change than those with relatively similar air and sea routes
(e.g., Canada). As Feyrer notes, “[such] heterogeneity can be used to generate a geography
based instrument for trade that varies over time.” In a similar vein, Feyrer (2009a)
exploits the shock to the global economy embodied by the closure of the Suez Canal from
1967 to 1975. While many trade routes remained unaffected, some did not and found the
distances separating markets increasing significantly. For instance, Feyrer reports that
India nearly led the pack with a 30.6% increase in its trade-weighted distance to foreign
markets while a country like Canada only experienced a 0.2% increase. Using this exogenous
variation in distance over time, Feyrer goes on to separately estimate the effect of
distance on trade and the effect of trade on income. Here, we combine both approaches. In
particular, we use the great circle distances from the CEPII GeoDist database (see
Appendix III) to represent distances on air routes to Japan, the United Kingdom, and the
United States, critical nodes of the world economy throughout the long twentieth century.
We also collect the corresponding distances for sea routes reported in Philip (1935).
Conveniently, this source also delineates which sea routes utilized the various major
canals of the world, e.g., the Kiel, the Panama, and the Suez.20 This information allows
us to incorporate changes in the distances of sea routes introduced by the various
closures and openings of these canals over the period from 1910 to 2010.21 The final step
is in constructing a series on the share of US imports by value which are transported by
air over this period based on Hummels (2007) and various reports of the International Air
Transport Association. Table 4 reports the results of this exercise using 4128 annual
observations for GDP per capita and market potential (our original sample of 4431
observations minus the 303 observations associated with Japan, the United Kingdom, and the
United States). The top panel of column (1) represents the first stage regression results.
In order of magnitude, effective distances to the United States, then Japan, and finally
the United Kingdom all register as statistically significant. Quantitatively, these three
instruments explain a significant amount of the variation in our measure of market
potential, with the R-squared of the regression registering a healthy 0.25. The regression
also passes a standard test of joint significance (Angrist-Pischke F test) where the null
hypothesis is that the endogenous regressors are jointly insignificant and a standard test
of under-identification (Angrist-Pischke underid. test) where the null hypothesis is that
any particular endogenous regressor is unidentified. The bottom half of column (1)
represents the second stage regression results. There, the elasticity between market
potential and GDP per capita is estimated to be 0.41, or about half the size of the
equivalent estimate reported in column (2) of Table 2. However, this elasticity is
precisely estimated and, in combination with the fixed effects, captures a majority of the
variation in GDP per capita across space and time. Furthermore, the second stage passes a
standard test of over-identification (Hansen J statistic) where the null hypothesis is
that the included instruments are uncorrelated with the error term and that the excluded
instruments are correctly excluded from the estimating equation. Again, we replicate the
same set of results as in previous tables by using full versus restricted samples (columns
(1) versus (2) and (3)) and by averaging dependent and independent variables over
increasingly large periods of time (columns (4) and (5)). All of the coefficients are
precisely estimated, fall within the range of 0.41 and 0.47, and are smaller than their
OLS counterparts, suggesting a potential role for endogeneity in driving our previous
results. At the same time, across all specifications a significant portion of the
variation in GDP per capita is explained by the instrumented version of our market
potential variable. Naturally, standard concerns regarding the exogeneity of our
instruments and the exclusion restriction may remain. We therefore prefer to interpret
these results as suggestive and not definitive. Nevertheless, they add to a growing body
of literature that provides evidence of causal effects arising from changes in market
potential. Apart from Feyrer (2009a, 2009b), this literature includes the contributions by
Hanson and Xiang (2004) who examine home market effects in the exports of OECD countries
across industries as well as Redding and Sturm (2008) who exploit the division of Germany
after World War II and its subsequent reunification.

<h>CONCLUSION</h>
----------

We develop a new approach to the old notion of market potential. Developing a structural
gravity model of trade, we show that market potential can be expressed as a function of
directly observable variables such as domestic trade flows and output and easily estimated
proxies for domestic trade costs. We derive this expression by solving for multilateral
resistance price indices across countries. These indices indirectly capture bilateral
trade costs and therefore contain variation that is essential for computing market
potential. Our approach has two key advantages. First, our measure is straightforward to
compute. As we do not need to add up exporter and importer fixed effect coefficients, it
offers an alternative to the more onerous construction of traditional market potential
measures. Second, our measure of market potential naturally lends itself to comparisons
over time, not only in the cross-section. On the empirical side, we construct market
potential measures for 51 countries over the period from 1910 to 2010. We find that market
potential exhibits an upward trend across all regions of the world from the early 1930s
and that this trend significantly deviates from the evolution of world GDP. Finally, we
also show that our measure of market potential is closely associated with average incomes,
both in the cross-section and over time and across various specifications. Most
importantly, we exploit exogenous variation in trade-related distances to world markets
generated from changes in logistics and transport technology along with geopolitical
events in order to assign a causal role for market potential in driving global income
growth over this period.


<h>REFERENCES</h>
----------

  [1] James E. Anderson, Eric Van Wincoop. Gravity with gravitas: A solution to the border puzzle. doi:10.1257/000282803321455214
  [2] James E. Anderson, Eric Van Wincoop. Trade costs. doi:10.1257/0022051042177649
  [3] Thibault Fally. Structural gravity and fixed effects. doi:10.1016/j.jinteco.2015.05.005
  [7] Gordon H. Hanson. Market potential, increasing returns and geographic concentration. doi:10.1016/j.jinteco.2004.09.008
  [9] Chauncy D. Harris. The, market as a factor in the localization of industry in the United States. doi:10.1080/00045605409352140
  [10] Keith Head, Thierry Mayer. Gravity, market potential and economic development. doi:10.1093/jeg/lbq037
  [12] David Hummels. Transportation costs and international trade in the second era of globalization. doi:10.1257/jep.21.3.131
  [13] David S. Jacks, Christopher M. Meissner, Dennis Novy. Trade booms, trade busts, and trade costs. doi:10.1016/j.jinteco.2010.10.008
  [14] P. Krugman. Increasing returns and economic geography. doi:10.1086/261763
  [16] Dan Liu, Christopher M. Meissner. Market potential and the rise of US productivity leadership. doi:10.1016/j.jinteco.2014.11.012
  [17] Dennis Novy. Gravity redux: Measuring international trade costs with panel data. doi:10.1111/j.1465-7295.2011.00439.x
  [19] Natalia Ramondo, Andrés Rodríguez-Clare, Milagro Saborío-Rodríguez. Trade, domestic frictions, and scale effects. doi:10.1257/aer.20141449
  [20] Stephen Redding, Peter K. Schott. Distance, skill deepening and development: Will peripheral countries ever get rich?. doi:10.1016/S0304-3878(03)00118-4
  [21] Stephen J. Redding, Daniel M. Sturm. The costs of remoteness: Evidence from German division and reunification. doi:10.1257/aer.98.5.1766
  [22] Stephen Redding, Anthony J. Venables. Economic geography and international inequality. doi:10.1016/j.jinteco.2003.07.001
  [23] J. M.C. Santos Silva, Silvana Tenreyro. The log of gravity. doi:10.1162/rest.88.4.641
  [24] Michael E. Waugh. International trade and income differences. doi:10.1257/aer.100.5.2093
<ART>Monetary-fiscal interactions with endogenous liquidity frictions
================================================================

Authors: Wei Cui
DOI: 10.1016/j.euroecorev.2016.03.007
Year: 2016  |  Pages: 1-25
ASJC codes: 2002, 2003
Keywords: Liquidity frictions, Monetary and fiscal interactions

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

I develop a tractable macro model with endogenous asset liquidity to understand monetary-fiscal interactions with liquidity frictions. Agents face idiosyncratic investment risks and meet financial intermediaries in competitive search markets. Asset liquidity is determined by the search friction and the cost of operating the financial intermediaries, and it drives the financing constraints of entrepreneurs (those who have investment projects) and their ability to invest. In contrast to private assets, government bonds are fully liquid and can be accumulated in anticipation of future opportunities to invest. A higher level of real government debt enhances the liquidity of entrepreneurs' portfolios and raises investment. However, the issuance of debt also raises the cost of financing government expenditures: a higher level of distortionary taxation and/or a higher real interest rate. A long-run optimal supply of government debt emerges. I also show that a proper mix of monetary and fiscal policies can avoid a deep financial recession.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Asset liquidity captures the ease with which financial assets can be traded without
strongly affecting their prices. The recent long-lasting world-wide financial crisis has
shown that liquidity fluctuations in asset markets can have a huge impact on asset prices
and the real economy.1 In fact, empirical evidence points to procyclical variation in the
liquidity of a wide range of financial assets.2 Understanding the frictions that generate
these fluctuations and the possible policy responses seems thus crucial. This paper
studies monetary–fiscal interactions when movements in asset prices and the real economy
are driven by endogenous fluctuations in liquidity. Although the research on
monetary–fiscal interactions at least go back to Sargent and Wallace (1981), Leeper
(1991), and Sims (1994),3 the consideration of endogenous liquidity frictions is usually
missing. To fill this gap, I incorporate these frictions into an almost standard New
Keynesian model with sticky prices. In the model, government bonds are fully liquid and
represent public liquidity, while privately issued claims, traded on competitive search
markets, are only partially saleable and have a bid-ask spread. Private claims represent
private liquidity and carry a liquidity premium, a premium that buyers will demand when
the assets cannot be easily converted into consumption goods at the fair market value. I
show that the government faces a tradeoff between the benefit of public liquidity
provision and the cost of financing government expenditures. Therefore, an optimal long-
run debt-to-GDP ratio can exist. When the economy is hit by large adverse financial
shocks, a proper mix of monetary and fiscal policies is the key to stabilize the economy.
In the model, private agents face idiosyncratic investment opportunities and there is no
insurance market for idiosyncratic risks. When an investment opportunity arrives, an agent
becomes an entrepreneur. Otherwise, she is a worker earning wages. The entrepreneur can
finance investment by issuing financial claims to the new capital stock and/or by
liquidating existing claims. Issuing or reselling private claims needs to go through
competitive financial intermediaries, which implement a costly search and matching
technology. The model׳s innovative aspect is the asset market structure. Asset liquidity
is endogenously determined in a competitive search environment where agents meet financial
intermediaries. Two important results emerge by endogenizing asset liquidity. First, the
model generates the positive co-movement between asset saleability and asset prices, as
observed in the data. The key aspect is that asset demand is endogenous and determines
saleability, tightness of financing constraints, and asset price jointly. Second,
government policies can affect the market structure and asset liquidity. As market- and
bank-based financial intermediation both share the essential feature of matching savers
and borrowers, our framework admits both interpretations of the intermediation process, as
in De-Fiore and Uhlig (2011). The financial frictions, induced by costly search, reduce
the amount of resources that are transferred to entrepreneurs with investment projects.
Therefore, if the liquidity of private claims is too low, private agents cannot fully
self-insure idiosyncratic risks. When fully liquid government bonds circulate, private
agents will purchase them as a buffer stock in case a good investment opportunity comes
up. Such precautionary savings reduce the real return from bonds and further raise
liquidity premium. I analyze a class of monetary and fiscal policy rules with long-run
targets suggested by actual policy practice. The monetary authority sets the nominal
interest rate as a function of current inflation and output. The fiscal authority chooses
a level of tax rate that depends on the quantity of real government debt; it can also
adjust government expenditures as a function of current debt and output. I first study the
long-run optimal supply of (real) government debt. The government faces a key tradeoff
when supplying government bonds. On the one hand, more (real) government debt implies more
public liquidity, which can be accumulated by agents awaiting investment opportunities and
enhances entrepreneurs׳ ability to carry out investment when the opportunity arises. The
financing constraints are less tight, thus reducing the liquidity premium of private
claims and further encouraging buyers entering the financial market. On the other hand,
more (real) government debt also implies a higher real interest rate and/or a higher tax
rate, raising the cost of financing government expenditures. After analyzing the long-run
economy, I turn to equilibrium dynamics after financial shocks. First, I study a simple
class of policy rules in which the monetary authority sets the nominal interest rate as an
increasing function of inflation only and the fiscal authority only adjusts the tax rate
but not government expenditures. Adverse financial shocks, modeled as rises in the search
costs, drive away the asset demand, reduce the saleability of private claims, and push
down their price. The financial shocks affect the bid-ask spread, as in Ajello (2012) and
Bassetto et al. (2015). Adverse financial shocks drive up the hedging value of liquid
assets and push workers towards them. The liquidity premium rises and the demand for
private claims falls: a flight to liquidity occurs. Entrepreneurs who issue private claims
are even more financing constrained. Therefore, demand for goods drops and firms produce
less. Such output contraction lowers agents׳ income expectation further, pushing them even
more towards liquid assets. We thus see persistent falls in investment, consumption, and
output. Because of less demand for physical investment after adverse financial shocks,
inflation falls and nominal interest rates drop. When the adverse financial shocks are
large, the nominal interest rate could drop to the zero lower bound (ZLB). With nominal
frictions, I show that large adverse financial shocks combined with the ZLB can generate a
much deeper recession, compared to the case when the ZLB is not a hard constraint.
Finally, I consider a more sophisticated class of policy rules. I allow the nominal
interest rate to be a function of both inflation and output, and allow the fiscal
authority to adjust government expenditures. The optimal policy responses to financial
shocks, within this class of monetary and fiscal rules, suggest an anticipated
expansionary fiscal contraction under which the ZLB does not constrain nominal interest
rates. In particular, an anticipated reduction of government expenditures “crowds in”
resources, relaxes entrepreneurs׳ financing constraints, and raises aggregate demand
immediately. Compared to the simple rule, such expansionary fiscal contraction (in
response to financial shocks) implies that the fiscal authority should be more
accommodating while the monetary authority needs to be more responsive to inflation.
Relationships to literature: This paper analyzes financial frictions based on Kiyotaki and
Moore (2012) and Shi (2015).4 The large family structure for simple aggregation in this
paper also follows Shi (2015). The presence of liquidity constraints opens up the
possibilities for government bonds or fiat money to circulate, which at least goes back to
Holmström and Tirole (1998). That is, if private liquidity is not enough, public liquidity
can be added to achieve efficiency.5 This paper provides a novel channel in which public
liquidity provision is costly due to distortionary taxation. Therefore, an optimal supply
of public liquidity emerges. Importantly, asset saleability and asset price are
endogenously generated from costly search and matching, thus avoiding the (counterfactual)
negative co-movement discussed in Shi (2015) and Bigio (2012) when asset saleability is
exogenous. A drop in asset demand reduces saleability of assets and their prices, thus
tightening financing constraints. This effect is similar to that from the random search
framework of Cui and Radde (2015), who focus on the fragility of financial markets. For an
survey of the literature using search in asset markets, see Rocheteau and Weill (2011) or
Lagos et al. (2016). Since the last financial crisis, nominal interest rates in many
developed economies have stayed at the ZLB. I show that why with liquidity frictions
adverse financial shocks can generate deflationary pressures and push nominal interest
rates to the ZLB (when the monetary authority follows a simple Taylor rule). In this
regard, this paper is a compliment to Eggertsson and Krugman (2012) and Buera and Nicolini
(2014). Two sets of policy tools have been proposed to deal with the ZLB. The first is
unconventional monetary policy or “Quantitative Easing” (QE).6 Del Negro et al. (2011)
demonstrate the large impact of liquidity fluctuation on investment and asset prices and
how unconventional monetary policies might stabilize the economy. The second proposal,
such as in Christiano et al. (2011) and Woodford (2011), argues that raising government
expenditures will not crowd out private consumption when the ZLB binds. I show that even
without the consideration of “QE”, the monetary–fiscal interactions are important when the
economy features liquidity frictions. Further, after adverse financial shocks, fiscal
expansion might not be better than fiscal contraction which crowds in resources, relaxes
financing constraints of some private agents, and raises aggregate demand. Government debt
provides liquidity service and has the “crowding-in” effect, similar to Woodford (1990).
This aspect is in contrast with Aiyagari and McGrattan (1998) in which government debt is
a perfect substitute to private assets (or capital stock). Government debt relaxes agents׳
borrowing constraints but also has the “crowding-out” effect on capital accumulation. In
Angeletos et al. (2013), government bonds also “crowd in” resources as they have a higher
level of exogenous pledgeability as collateral than capital assets. This paper, however,
features asset saleability (and a bid-ask spread) instead of asset pledgeability. In
addition, I show that public liquidity provision can also alter the liquidity of privately
issued claims through the endogenous search and matching.

<h>THE MODEL</h>
---------

I construct a growth model with liquidity frictions and nominal price stickiness. The
economy is populated by a continuum of similar households (with measure one), firms,
financial intermediaries, and a government. Time is discrete and infinite. Each period is
divided into four sub-periods. (1) The households׳ decision period. The shocks to
aggregate productivity At (TFP shocks) and to intermediation search cost κt (financial
shocks) are realized. All members in a representative household equally divide the
household׳s financial assets consisting of government bonds and privately issued financial
claims on capital stock. The household instructs its members on the optimal type-specific
choices to be carried out after individual types (explained below) have been realized. (2)
The production period. Each member receives a status draw, becoming an entrepreneur (type
i) with a probability χ and a worker (type n), otherwise. Workers supply labor hours,
while only entrepreneurs have access to investment projects transforming consumption goods
into capital stock one-for-one. Intermediate goods firms, in a monopolistically
competitive market, rent capital stock Kt and labor Nt from the household to produce
intermediate products. The after-tax rental rate and wage rate are rt and Wt. Final goods
firms produce numeraire consumption goods by aggregating intermediate products. The
profits (Dt) from intermediate goods firms are equally distributed among members. (3) The
investment period. There is no insurance among household members, and they keep separated
until the consumption stage. Because of the equal division of assets in the beginning,
entrepreneurs are financing constrained in investment. They seek outside financing.
Financial markets open in which entrepreneurs offer financial claims for sale and workers
purchase these claims through financial intermediaries, which implement a costly search
and matching technology. Search frictions imply that private financial claims are only
partially liquid. In contrast, government bonds are fully liquid as they can be traded on
a frictionless spot market. Financial intermediaries are competitive and search in
financial submarkets. Entrepreneurs and workers choose the best financial market subject
to the participation constraints of financial intermediaries. The competitive search
process shares similar features with that in the labor search literature such as Moen
(1997). (4) The consumption period. Entrepreneurs and workers reunite again in their
respective households, pool all assets together, and share consumption goods across all
members. Throughout the paper, I focus on the type of equilibrium in which entrepreneurs
are financing constrained and both private claims and government bonds circulate. I verify
the existence of such type of equilibrium in the numerical analysis.

<hs>  A representative household</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~

Note that there is no currency, which is another form of public liquidity in practice. One
can give fiat money an extra role, for example, by having money in the utility of the
household. Nevertheless, a higher level of money or government debt does not necessarily
mean more liquidity. Public liquidity here means real liquidity which has to be eventually
backed by the government׳s primary surplus. What is important is the real value of
liquidity, whether it is in the form of government bonds or in the form of money. For this
reason and for simplicity, I mix government bonds and money.

<hs>  Asset price and asset liquidity</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

There is a continuum of competitive financial intermediaries, each of which chooses on
which submarket to collect and match quotes at per-quote costs of κ units of consumption
goods. The probability of filling a buy quote is fm, while the probability of filling a
sell quote (or asset saleability) is ϕm.

<hs>  Firms</hs>
  ~~~~~

The production sector consists of intermediate goods firms and final goods firms, as in a
standard New Keynesian model such as in Leeper et al. (2012) and references therein. To
simplify, I only incorporate sticky prices using the Calvo type of price adjustment.

<hs>  Government policies and the transformed economy</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The government follows policy rules which are taken as given by private agents. I restrict
to a class of policy rules that have long-run targets and induce a balanced growth path.
For this reason, the “long-run equilibrium”, the “steady state”, and the “balanced-growth
path” are used interchangeably.

<hs>  Recursive equilibrium</hs>
  ~~~~~~~~~~~~~~~~~~~~~

Now, I close the model by defining the recursive equilibrium. Readers who are not
interested in the technical definition can skip this subsection.

<h>LIQUIDITY PREMIUM AND THE COST OF PUBLIC LIQUIDITY PROVISION</h>
------------------------------------------------------------

In this section, I characterize the equilibrium analytically. The government can provide
public liquidity (real government debt) to mitigate the liquidity frictions. When private
liquidity is in shortage due to the search frictions, public liquidity can be used as an
alternative. A higher level of public liquidity means that entrepreneurs with government
bonds become richer and can invest more, according to the investment equation (11). It can
also reduces the liquidity premium through the endogenous search market structure, as
entrepreneurs rely less on the outside financing. Then, I show that public liquidity
provision is, however, not free because of the distortionary taxation. When the government
sets long run targets, it faces the tradeoff between the benefit of public liquidity
provision and the cost of government financing.

<hs>  Liquidity premium and asset price</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Now, I study the relationship between asset saleability and asset price. One shall see
that whether a lower level of the equilibrium saleability ϕ is associated with a higher or
a lower asset price qi depends on the relative strength of asset supply and demand
effects. On one hand, a lower level of ϕ implies tighter financing constraints and less
supply relative to demand on the asset search market as shown by Shi (2015). Then, the
shadow value of private claims rises. As intermediaries have to offer better conditions to
attract scarce supply, this should be reflected in a higher equilibrium asset price. On
the other hand, lower equilibrium asset saleability implies that private claims are less
effective investments to hedge future funding needs, which would reduce demand, increase
the equilibrium liquidity premium, and compress the asset price.

<hs>  Costly public liquidity provision</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Since private claims do not have enough liquidity, the government can provide public
liquidity to mitigate liquidity frictions. But public liquidity provision is costly, as
there is a tradeoff between the benefit of public liquidity provision and the cost of
government financing. Intuitively, since private claims carry a liquidity premium and
government bonds are scarce, precautionary entrepreneurs tend to push down the real
interest rate compared to the case without liquidity frictions. Consequently, the (real)
price of bonds are unnecessarily high, and the government needs to supply more real
government debt. Given a qn, this public liquidity provision also reduces the liquidity
premium in (34), as entrepreneurs rely less on the financial market but more on public
liquidity. In later numerical analysis, I will show that these effects still hold in
general equilibrium. The above discussion suggests that liquidity premium has a negative
impact on financing investment. On the contrary, if government expenditures need to be
financed at the same time, some degree of liquidity premium is preferred by the fiscal
authority. One possible way to see this is that, a higher real interest rate implies that
government expenditures become more expensive to finance. With a higher real interest
rate, the government with a high level of real government debt will have to either cut
government expenditures (which reduces the social welfare that depends on public
spending), or raise more distortionary taxation.

<hs>  Calibration</hs>
  ~~~~~~~~~~~

The model is calibrated in quarterly frequency to match several US long-run statistics.
The calculation of steady state can be found in Appendix A.

<hs>  The optimal debt-to-GDP ratio</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

With more public liquidity, workers search less private liquidity such that the
equilibrium asset saleability falls. But at the same time entrepreneurs are less financing
constrained, and the representative household is thus more willing to consume. As
consumption rises with the debt-to-GDP ratio, leisure increases (hours worked fall)
because they are complements. One interesting feature is that output is non-monotone. The
drop of labor hours reduce output initially, but output rises with the debt-to-GDP ratio
because the cut in expenditures “crowds in” investment and production. Importantly,
although the public liquidity provision mitigates financial frictions, the cut in
government expenditures will eventually reduce the social welfare with the rise of debt-
to-GDP ratio (for a given ψg). The consumption-equivalence welfare gains are about 1.1% if
the debt-to-GDP ratio is 0.6 (the calibrated level) and about 0.6% if the debt-to-GDP
ratio is 1.0. Therefore, the parameter ψg is chosen such that welfare is maximized at the
calibrated debt-to-GDP ratio. In sum, facing liquidity frictions, the monetary authority
prefers a higher real interest rate and public liquidity provision, as it will attenuate
liquidity frictions. Nevertheless, financing government expenditures becomes more costly
with a higher real interest rate. The fiscal authority thus prefers a lower interest rate.
The conflicts then imply both an optimal real interest rate and an optimal level of
government debt that balance the tradeoff.

<h>EQUILIBRIUM DYNAMICS AND MONETARY–FISCAL INTERACTIONS</h>
-----------------------------------------------------

First, I study a special and simple class of rules in (24), in which the monetary
authority sets the nominal interest rate only as a function of inflation, while the fiscal
authority adjusts taxes in response to the level of real government debt outstanding. The
simple rules are fairly standard in the literature. Then, I move to discuss the scenario
when the government is able to follow the full set of rules in (24).

<hs>  A simple class of monetary and fiscal rules</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

This division is similar to Leeper (1991), who points out that both monetary policy and
fiscal policy can be labeled as either active or passive. Being active means that the
authority is forward looking and is not constrained by the current government budget
constraint; it is free to choose a rule. Being passive means that it is backward looking
and is constrained by the active authority and the private agents׳ behaviors. An economy
system has a locally unique stable equilibrium if and only if one authority is active and
the other authority is passive. Therefore, region I is the active monetary–active fiscal
(AM + AF) regime, while region II is the passive monetary–passive fiscal (PM + PF) regime.
Region III combines both active monetary–passive fiscal (AM + PF) and passive
monetary–active fiscal (PM + AF) regimes. The reason for such non-linear region boundaries
is that liquidity frictions together with sticky prices generate non-trivial inflation and
liquidity premium dynamics after shocks. The monetary–fiscal interaction is more
complicated than a model without liquidity frictions. Next, I discuss the details.

<hs>  Simple policy rules and shocks</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

On the contrary, when there are only negative TFP shocks, the return from investment is
persistently low and the need for investment drops. Therefore, negative TFP shocks reduce
liquid assets׳ hedging value for future investment (given that there are no financial
shocks). The difference can be clearly seen in the liquidity premium dynamics after the
two shocks. Adverse financial shocks push up liquidity premium, while negative TFP shocks
do the opposite. After the financial shocks, flight to liquidity pushes up liquidity
premium which dominates the increase of marginal product of capital such that asset price
falls. This channel avoids the rise of asset price generated by an exogenous fall of ϕ as
noted by Bigio (2012) and Shi (2015). TFP shocks, however, generate smaller declines in
asset saleability in the initial periods. This is because a persistent lower TFP, albeit
pushing down liquidity premium, reduces rental rates of capital and also generates
persistent falls in the demand for private claims and asset price. Note that asset price
and asset liquidity affect investment, since entrepreneurs use the financial market to
leverage their net worth for investment projects. The drop of asset price qi and
saleability ϕ tightens entrepreneurs׳ financing constraints. That is why financial shocks
have a significant impact on investment (with a 5% initial drop) compared to TFP shocks
(with a 3% initial drop). Note that the consumption movement after financial shocks is
affected by nominal rigidities. In the previous literature without sticky prices,
investment and consumption usually move in opposite directions after negative financial
shocks (Kiyotaki and Moore, 2012 and Shi, 2015). The drop of output is small and only
limited to the forgone capital accumulation. With nominal rigidities, “flight to
liquidity” reduces inflation and increases real wages. Intermediate goods firms thus find
it optimal to reduce labor hours. Then, output falls immediately together with a sharp
decline of investment. That is why consumption does not need to rise and move in the
opposite direction of investment (except for the first two periods as we have a moderate
degree of price stickiness). After financial shocks, workers invest more in liquid assets
which are not backed by real investment. Therefore, capital accumulation significantly
slows down and the total net worth of the economy falls, which further exacerbates the
financing situation of entrepreneurs in the future. Anticipating this, workers further fly
to liquidity which causes persistent reduction of investment, consumption, and output.

<hs>  The impact of zero lower bound after financial shocks</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The previous exercise suggests that the nominal interest rate could drop below zero, when
adverse financial shocks are large enough to generate a high deflationary pressure.
Nevertheless, the zero lower bound (ZLB) seems to be a crucial technical constraint, as
agents will prefer to hold money if the nominal rate is below zero. In my model, the ZLB
will be important as product prices are sticky. If constrained by the ZLB, which is a hard
constraint,9 the nominal interest rate can further affect policies and the real economy
activities. Importantly, the ZLB amplifies the effect of financial shocks: the constraint
is binding in a given period, and agents expect it to be binding in the future. This
belief lowers expected future income and net worth and generates deflationary
expectations. Such expectation leads to a rise in real rates and a fall in demand.
Therefore, workers prefer to save in liquid government bonds and reduce consumption
further. This again reduces the demand for private claims and their saleability, and
entrepreneurs find it even harder to finance investment projects. As a result, asset price
drops significantly more if the ZLB binds. Note that the ZLB brings up the real interest
rate when inflation falls, and the fiscal authority needs to raise more taxes and issue
more government debt to finance the interest payments. This effect further distorts the
economy. Liquidity premium increases less when the ZLB binds, reflecting that the fiscal
authority finds it more costly to finance government expenditures. The above exercise
complements the studies by Eggertsson and Krugman (2012) and Buera and Nicolini (2014) in
which they argue that the hit of ZLB is because of tightening of borrowing constraints.
Here, adverse financial shocks are similar to the tightening of borrowing constraints as
issuing and/or reselling assets are harder and more costly. Agents fly to liquidity,
reduce aggregate demand, and push down inflation. Then, the monetary authority
significantly reduces the nominal interest rate, which could stay at zero for a long
period of time.

<hs>  Optimal simple and sophisticated policy rules</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Since the unconditional expectation of average household utility can be expressed as the
weighted unconditional variances of output, inflation, consumption, investment, and
government expenditures, I search for the coefficients which minimize the unconditional
variances. As a comparison, I also compute the optimal policy parameters when the
government is constrained to the simple rules. The difference can be seen from the optimal
policy parameters in Table 3. One might view that fiscal expansion is always helpful in
stabilizing inflation, since it can raise aggregate demand when inflation is low. This
point is argued by Christiano et al. (2011) and Woodford (2011) when nominal interest
rates are at the ZLB. Nevertheless, anticipated fiscal contraction can also raise
aggregate demand when entrepreneurs are financing constrained. Agents expect that future
fiscal contraction gives back resources to entrepreneurs, thus relaxing financing
constraints and raising the demand for investment in the future. Workers are more willing
to search for investment projects, relaxing entrepreneurs׳ financing constraints today.
Therefore, entrepreneurs can invest more today, and households accumulate more capital and
find themselves richer in the future, which further encourages workers to search for
investment projects today. That is, in the simulation, the fiscal contraction׳s effect
dominates the fiscal expansion׳s effect in raising demand, as endogenous financing
constraints are powerful in amplification. The important consequence of this transmission
is that inflation is stabilized even if the economy is hit by large financial shocks.
Under the sophisticated policy rules, however, inflation is stable and real interest rates
drop after shocks. That is why liquidity premium increases more than that under the simple
policy rules while the real debt burden only increases slightly. The tradeoff between the
benefit of public liquidity provision and the cost of government financing is less severe
when agents fly to liquidity and government expenditures fall. The increase of the real
value of debt is mostly from the voluntary drop of government expenditures, instead of
from the drop of nominal price levels. By using fiscal contraction, the government
maintains a healthy increase of public liquidity provision. As a result, the rise in
distortionary taxation is moderate (Fig. 5). In sum, the monetary authority is more active
than what the simple rules imply. However, it is unlikely constrained by the ZLB even if
the economy is hit by very large financial shocks. Although the government is constrained
by policy rules in the model, a careful mix of monetary and fiscal policies can avoid the
deep recession generated by liquidity frictions and the ZLB. Remark: I do not analyze the
optimal taxation in these policy experiments. First, fixing the tax rule is relatively
simple. Perhaps, in practice, it is indeed hard to change taxation within a short period
of time, while adjusting government expenditures is easier. Second, if the fiscal
authority can adjust tax rules, one might view that it is better to provide real liquidity
right after shocks by promising higher tax rates in the future. However, it is unlikely
that such policy is better than the sophisticated rules, since it requires a higher level
of distortionary taxation and is subject to more severe commitment issues.

<h>CONCLUSION</h>
----------

I illustrate the importance of monetary–fiscal interactions with endogenous liquidity
frictions. In particular, the tradeoff between the benefit of public liquidity provision
and the cost of financing government expenditures implies an optimal long-run supply of
government debt. In combating large adverse financial shocks, the proper mix of monetary
and fiscal policies can avoid the zero lower bound on nominal interest rates under a
simple Taylor rule. For simplicity, the paper assumes government debt as a blend of non-
interest and interest bearing liabilities. Future research can give an explicit role for
fiat currency and/or reserves of central banks. At the same time, I assume “private
claims” as an amalgam of privately issued equity and debt. One could further analyze a
more realistic capital structure and the implication for monetary–fiscal interactions.
Finally, further work could also focus on the government commitment issues (for example
illustrated in Bassetto, 2005) when government debt provides liquidity services.


<h>REFERENCES</h>
----------

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  [13] Bengt Holmström, Jean Tirole. Private and public supply of liquidity. doi:10.1086/250001
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  [29] Michael Woodford. Interest and prices: Foundations of a theory of monetary policy
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  [32] Marco Bassetto. Equilibrium and government commitment. doi:10.1016/j.jet.2004.06.001
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<ART>Monetary policy under behavioral expectations: Theory and experiment
====================================================================

Authors: Cars Hommes, Domenico Massaro, Matthias Weber
DOI: 10.1016/j.euroecorev.2019.05.009
Year: 2019  |  Pages: 193-212
ASJC codes: 2002, 2003
Keywords: Behavioral macroeconomics, Experimental macroeconomics, Heterogeneous expectations, Learning-to-forecast experiment

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Expectations play a crucial role in modern macroeconomic models. We consider a New Keynesian framework under a behavioral model of expectation formation and under rational expectations. Contrary to the rational model, the behavioral model predicts that inflation volatility can be lowered if the central bank reacts to the output gap in addition to inflation. We test the opposing theoretical predictions in a learning-to-forecast experiment. In line with the behavioral model, the results support the claim that output stabilization can lead to less volatile inflation.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Expectations play a crucial role in modern macroeconomic theory. Standard models used for
scientific research and policy analysis typically assume a representative fully rational
agent. However, the assumption that all agents in an economy are fully rational and able
to determine the model-consistent expectation of the underlying process governing real-
world economic outcomes is highly problematic. A great deal of research has shown that
humans generally do not react fully rationally to the world around them. This research
ranges from providing evidence for simple biases to showing the inability of humans to
work with probabilities and to forecast future economic behavior (Tversky and Kahneman,
1974, and Grether and Plott, 1979, are seminal early contributions, and many have followed
since; see Camerer et al., 2011, for an overview). Moreover, the claim based on
evolutionary arguments that behavior deviating from the homogeneous rational expectations
solution will be driven out of markets over time has not held up to scrutiny (Brock and
Hommes, 1997; Brock and Hommes, 1998; De Grauwe, 2012a; see also Arthur et al., 1997). In
this paper we consider a standard macroeconomic model under both behavioral and rational
expectations. We examine aggregate macroeconomic behavior and policy implications arising
from the alternative assumptions on expectation formation, paying particular attention to
price stability. The behavioral model of expectation formation is a heuristic switching
model developed over a long period of time based on (mainly microeconomic) research
investigating how people form expectations and how they adapt them over time. Models of
this kind perform well in describing expectation dynamics using both survey and
experimental data (e.g., Branch, 2004; Hommes, 2011; Assenza et al., 2018). A key
difference in outcomes between the macroeconomic models with behavioral and rational
expectations concerns price stability, that is inflation volatility. Assuming rational
expectations, there is a clear trade-off for a central bank between fighting inflation
volatility and output gap volatility. If the central bank reacts to the output gap in
addition to inflation, under rational expectations this will result in an increase of
inflation volatility. The outcome is different under behavioral expectations. Starting
from a situation in which the central bank does not react to the output gap at all, the
central bank can simultaneously decrease inflation volatility and output gap volatility by
reacting to the output gap. However, inflation volatility as a function of the extent of
output gap reaction is U-shaped. This means that reacting to the output gap on top of
inflation will only lower inflation volatility up to a certain point, after which
inflation volatility starts to increase again. These different outcomes regarding
inflation volatility can be tested in the laboratory. We design a learning-to-forecast
experiment where the only difference between treatments consists in the monetary policy
rule used by the central bank. In one treatment, the central bank only reacts to
inflation, while in the other it also reacts to the output gap. Our experimental results
support the claim that inflation volatility can be lowered when the central bank also
reacts to the output gap, in line with the predictions of the behavioral model. Our
results from the behavioral model and the experimental data have clear policy implications
for central banks whose sole aim is to achieve price stability, such as the European
Central Bank (many other central banks, including those of New Zealand, Canada, England,
and Sweden, have a hierarchical mandate with price stability as the primary objective for
monetary policy). Even if these banks ultimately only care about price stability, this
goal is better achieved if they also react to changes in the output gap. This is important
and at odds with standard macroeconomic thinking built upon full rationality. Our work
mainly relates to two streams of literature. Firstly, it relates to the literature on
behavioral macroeconomics and learning in macroeconomics, for example Marcet and Nicolini
(2003), Orphanides and Williams (2006), Branch and McGough (2009, 2010), Woodford (2010),
De Grauwe (2011, 2012a, 2012b), De Grauwe and Kaltwasser (2012), Anufriev et al. (2013),
Kurz et al. (2013), Benhabib et al. (2014), and Bertasiute et al. (2018); see Evans and
Honkapohja (2001) and Woodford (2013) for overviews. In particular, our paper is not the
first to derive a non-monotonic relationship between inflation and output gap volatility.
De Grauwe (2011, 2012a) obtains a similar result in a different macroeconomic model with
simple behavioral rules of expectation formation. Moreover, Kurz et al. (2013) show that
the trade-off between inflation and output gap volatility is non-monotonic under rational
diverse beliefs (see Kurz, 2009, for a survey on rational diverse beliefs). Branch et al.
(2009) present similar findings in sticky information economies in which the degree of
attentiveness or the rate at which agents update their information is endogenized. The
main contribution of our paper is the empirical test of policy trade-offs by means of a
learning-to-forecast laboratory experiment. To our knowledge, our results are the first
experimental evidence for the missing trade-off between inflation and output gap
volatility. Secondly, our research relates to the literature on experimental
macroeconomics and learning-to-forecast experiments, for example Marimon and Sunder
(1993), Kelley and Friedman (2002), Lei and Noussair (2002), Arifovic and Sargent (2003),
Adam (2007), Heemeijer et al. (2009), Bao et al. (2012), Kryvtsov and Petersen (2013),
Cornand and M’baye (2018), Pfajfar and Zakelj (2014), Assenza et al. (2018), and Hommes et
al. (2019); see Duffy (2012), Assenza et al. (2014), and Cornand and Heinemann (2014) for
reviews. Most closely related to our paper are the learning-to-forecast experiments of
Pfajfar and Zakelj (2014) and Assenza et al. (2018), which are framed in a setup similar
to ours. The first paper studies inflation expectation formation under different interest
rate rules reacting only to inflation, finding that rationality of expectations can be
rejected for the majority of participants. We focus instead on the policy trade-off
between inflation and output gap volatility, comparing experimental outcomes when the
central bank only targets inflation and when it also targets the output gap. Another
important difference concerns the experimental design. While in Pfajfar and Zakelj (2014)
participants forecast inflation only, we allow subjects to forecast both inflation and the
output gap, in accordance with the theoretical macroeconomic model underlying the
experiment. Assenza et al. (2018) consider participants forecasting both inflation and the
output gap but focus on the Taylor principle as a device to pin down inflation dynamics.
This paper is organized as follows. In Section 2 we describe how we model the economy and
the formation of expectations. We also show the main differences between the rational and
behavioral versions. In Section 3 we first describe the experimental design and the
procedures. Then we show the experimental results. Section 4 concludes.

<h>THEORY</h>
------

In this section, we first describe the underlying macroeconomic model. Then we introduce
the behavioral model of expectation formation. After that, we compare the outcomes of both
models and describe the economic intuition behind these outcomes.

<hs>  A behavioral model of expectation formation</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Models with rational expectations are based on the assumption that agents have perfect
information and a full understanding of the true model underlying the economy. There is,
however, a large body of empirical literature documenting departures from this assumption.
Furthermore, in survey data there is usually a high variance of inflation forecasts (e.g.,
Carroll, 2003; Mankiw et al., 2003; Branch, 2004) strongly suggesting that expectations
are heterogeneous. Existing literature on expectation formation shows that many people use
heuristics to make forecasts of future (macroeconomic) variables. This behavior is not
necessarily a consequence of agents’ irrationality; it can also be a “rational” response
of agents who face cognitive limitations and have an imperfect understanding of the true
model underlying the economy (e.g. Gigerenzer and Todd, 1999; Gigerenzer and Selten,
2002). Next, we introduce a behavioral model of expectation formation for such an
environment.

     <hss>Robustness and measurement of inflation volatility</hss>

        The simulation results are qualitatively robust to a wide variety of changes. This
        includes changes in all parameters of the macroeconomic model. It also includes
        changes in the parameters of the behavioral model of expectation formation. More
        interestingly, the results are also robust to other models of behavioral
        expectation formation, such as a heuristic switching model with fewer and simpler
        heuristics or adaptive expectations without any switching involved. Also if the
        central bank uses a slightly different Taylor rule to smooth the interest rate,
        the results persist (more precisely, we model the interest rate rule in that
        exercise as a weighted average of the regular Taylor rule and the previous
        period’s interest rate). Such variations are shown in Online Appendix B. While the
        results are qualitatively robust to these changes within this macroeconomic
        framework (which is the most standard framework for macroeconomic policy
        analysis), it is possible in other macroeconomic frameworks to reverse the results
        obtained by rational expectations. That is, it is possible to obtain a reduction
        of inflation volatility by increasing ϕy; an example are models that only include
        shocks to the aggregate demand equation (1) such as technology shocks, preference
        shocks or variations in government purchases, but do not include shocks to the
        short-run aggregate supply relationship (2) (see Woodford, 2003). In such
        frameworks, behavioral expectations are an additional reason why inflation
        volatility decreases when also targeting the output gap. One of the reasons why
        the mean squared deviation from the target may be popular among economists is that
        it constitutes a welfare criterion under homogeneous expectations. However, as
        shown in Di Bartolomeo et al. (2016), it is not an appropriate welfare criterion
        when agents have heterogeneous expectations. In this case, price dispersion arises
        not only because of the staggered price setting mechanism but also because of the
        heterogeneity of prices set by reoptimizing firms in the Calvo lottery, which
        depends on the heterogeneity of firms’ expectations of future inflation. In our
        behavioral model, this heterogeneity increases in the relative changes in
        inflation. In general, reducing inflation volatility by means of an interest rate
        rule that reacts to both inflation and output gap fluctuations, is thus welfare
        improving not only because it reduces the price differences between optimizing and
        non-optimizing firms, but also because it reduces the cross-sectional variance of
        prices set by optimizing firms. We refrain from using the precise welfare
        criterion as it depends on more than inflation alone. While welfare criteria
        derived in particular models may have influenced the fact that price stability is
        now the sole aim of many central banks, these central banks now have the mandate
        to achieve price stability and not the aim of maximizing a model-dependent welfare
        criterion. In addition, using a composite welfare measure would reduce the clarity
        and readability of the paper. Note that both simulation results and experimental
        results are similar when considering the precise welfare criterion.

<h>EXPERIMENT</h>
----------

The only task for subjects in the experiment is to forecast inflation and output gap.
These forecasts are then used to calculate subsequent realizations. The model underlying
the experimental economy is the macroeconomic model described in Section 2.1 (with the
same calibration of macroeconomic parameters as before). Before we describe the experiment
in more detail, we now explain the treatments and hypotheses. The design of the experiment
and the hypotheses can be motivated with the theory described in Section 2.

<hs>  Treatments and hypotheses</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~

We are interested in testing the null-hypothesis (which can be derived from the rational
expectations model in Section 2) that inflation volatility in T1 is less or equal to
inflation volatility in T2 against the alternative hypothesis (which can be derived from
the behavioral model) that inflation volatility is greater in T1 than in T2. Fig. 3
summarizes these hypotheses.

<hs>  Course of events and implementation</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The experiment was programmed in Java and conducted at the CREED laboratory at the
University of Amsterdam. The experiment was conducted with 258 subjects recruited from the
CREED subject pool (43 groups of six subjects each, distributed over thirteen sessions).
After each session, participants filled out a short questionnaire. Participants were
primarily undergraduate students, the average age was slightly above 22 years. About half
of the participants were female, about two-thirds were majoring in economics or business,
and about half were Dutch. During the experiment, ‘points’ were used as currency. These
points were exchanged for euros at the end of each session at an exchange rate of 0.75
euros per 100 points. The experiment lasted around two hours, and participants earned on
average about 30 euros. The series of error terms used in the model equations (gt and ut
in Eqs. (1) and (2)) differed across groups within each treatment, but the sets of noise
series used in the two treatments were the same.8

<hs>  Results</hs>
  ~~~~~~~

There are data of 43 different groups, 21 in T1 and 22 in T2. The groups’ actions do not
influence one another in any way; thus the observations at the group level are
statistically independent. The data for all groups separately including all individual
forecasts can be found in the Online Appendix E.

     <hss>Inflation</hss>

        Fig. 5 gives an overview of realized inflation in all experimental economies,
        separately for T1 and T2. Each line corresponds to the inflation in one economy,
        tracked over all 50 periods of the experiment. Almost all economies are close to
        the inflation target after 50 periods, and in the economies with inflation still
        oscillating around the target the amplitude of these oscillations is decreasing.9
        Groups are heterogeneous, with some groups exhibiting much larger volatility than
        other groups. In many groups in both treatments, inflation is within one
        percentage point from the target in most or all periods. Inflation generally
        fluctuates around its target: mean inflation is between 3.13 and 4.33 in T1 and
        between 2.79 and 3.82 in T2 (treatment averages of mean inflation are 3.55 in T1
        and 3.41 in T2). On average, inflation fluctuates a bit less in T2 than in T1, as
        predicted by the behavioral model.10

        The heuristic switching model as predictor of subjects’ forecasts

        After having analyzed the economic outcomes, we now examine the performance of the
        heuristic switching model used to derive the predictions in the experiment. Does
        this model accurately describe subjects’ forecasts? Or does the rational
        expectation solution or one of the heuristics alone predict subjects’ forecasts
        better than the switching model? In addition, we compare the prediction
        performance to that of a few parsimonious heuristic switching models. We report
        the prediction performance of the heuristic switching model (HSM), the performance
        of the homogeneous rational agent solution (RE) and the performance of the four
        heuristics involved in the switching model without any switching: adaptive
        expectations (ADA), weak trend-following (WTR), strong trend-following (STR), and
        the learning, anchoring and adjustment rule (LAA). In addition, we compare the
        model to four parsimonious heuristic switching models, namely one where agents
        switch between using naive expectations and using a trend-following rule with
        coefficient one (Naive+Trend), one where agents switch between forecasting the
        steady state and a trend-following rule with coefficient one (Fundamental+Trend),
        and models where agents switch between the steady state plus a constant and the
        steady state minus a constant (Biased Fund.; we use three different constants,
        0.25, 0.5, and 1). We use the mean squared difference between the models’ two-
        period ahead predictions and average forecasts in a group as prediction error. The
        predictions are thus out-of-sample predictions. In the main heuristic switching
        model, we use the same parameters as in Section 2 (that is, we use a preexisting
        calibration that is not influenced by our experimental data; for the parsimonious
        switching models, we use the same parameters unless otherwise specified). To form
        the predictions of the heuristic switching model, the fractions of agents using
        the different heuristics need to be determined. For this, we use the fractions
        that are implied by the theoretical model with a continuum of agents. We use the
        squared difference between this prediction and a group’s average forecast, because
        there are no degrees of freedom with this method.15 Table 2 shows average
        prediction errors across all periods and all groups in a treatment. Table 2 shows
        that, across the board, the benchmark model performs much better than rational
        expectations. Also evident in the table is that the rational expectation solution
        is a worse predictor in all cases than any of the four involved heuristics alone.
        Furthermore, the switching model is a better predictor in all cases than any of
        the four heuristics alone. In general, the differences are considerable. The
        switching model does much better than most of the other models. There are two
        heuristics that do very well when employed alone: the weak trend-following rule
        and the anchoring and adjustment rule. Nevertheless, the switching model predicts
        all four forecasts better than these heuristics. The prediction errors of these
        two best-performing heuristics when employed alone are always at least 25% greater
        than the prediction errors of the switching model. In addition, the main heuristic
        switching model does better throughout than the smaller switching models (that
        also have prediction errors of at least 25% above the benchmark model). Note that
        we are not attempting to fit the parameters of the heuristic switching model to
        the data ex post, as this would only give us lower prediction errors at the cost
        of adding degrees of freedom and thereby make the comparison with the homogeneous
        rational agent solution uneven.

     <hss>Fractions of heuristics used</hss>

        In the following, we consider the fractions of employed heuristics in the model
        fitted to the experimental data. This can help to understand which heuristics are
        used most and whether there are patterns concerning the use of the heuristics over
        time. Fig. 11 shows the fractions of the heuristics over time for inflation and
        output gap in T1 and T2 (the lines represent averages across groups). One can see
        that all heuristics have some support in the experiment. One can also see that the
        graphs of inflation and output gap forecasting in T1 are very similar. The same
        holds for the corresponding graphs in T2. This suggests that while subjects learn
        and update over time the way that they form expectations, they form expectations
        on inflation and output gap in similar ways, and change how they form expectations
        on inflation and output gap in similar ways. This is not self-evident: it could
        well have been the case that subjects rely more on trend extrapolation for one
        variable while behaving adaptively when forecasting the other variable. Regarding
        the use of the heuristics themselves, the adaptive rule and the anchoring and
        adjustment rule are used more often than the trend-following rules. The use of the
        adaptive rule increases over the course of the experiment, partially explaining
        the learning observed in the experiment. Furthermore, the trend-following rules
        are used less and less as the experiment proceeds (for inflation and output gap
        alike in both treatments; there are some small upward movements toward the end of
        the experiment in T1, however). This also contributes to the stability of
        inflation and output gap in the second half of the experiment, as the trend-
        following rules are destabilizing. The use of the anchoring and adjustment rule
        follows a less-clear pattern. It increases strongly in the beginning in T1 and
        decreases again thereafter. In T2 the use of this rule increases more slowly;
        afterwards, it levels off. This rule, which has two components, has a less clear-
        cut interpretation than the other rules. One component is destabilizing, taking
        into account last trends rather than predicting a return to the anchor
        immediately, while the other component, the anchor itself, is stabilizing, as the
        long-run averages are very close to the inflation target and the steady state of
        the output gap. It is interesting to see that, overall, relatively little use is
        made of the weak trend-following rule. While this rule alone predicts group level
        aggregates of forecasts rather well (Table 2), when looking at it from the point
        of view of the heuristic switching model, it seems that this is only the case
        because it approximates the prevailing mixes of the whole set of heuristics.

<h>CONCLUDING REMARKS</h>
------------------

We have conducted a learning-to-forecast experiment to test the predictions of a
macroeconomic model with behavioral expectations. This behavioral model yields results
that differ from those of the same macroeconomic model based on rational expectations.
Namely, the behavioral model yields that inflation volatility can be reduced if the
central bank reacts to the output gap on top of inflation. The predictions of the
behavioral model are supported by the outcomes of our experiment, in which the only
treatment variation consists in a modification of the central bank’s monetary policy
reaction function. These results are relevant for monetary policy analysis. They show a
different relationship between inflation and output-gap than is usually assumed. The
policy implications are particularly straightforward for central banks that aim at price
stability alone, such as, for example, the ECB; these central banks should react to the
output gap even if they are ultimately only interested in price stability. Note that our
policy recommendation has a broad foundation. We obtain it not only with our behavioral
benchmark model but also assuming a variety of other specifications of expectation
formation (as outlined in Online Appendix B). Moreover, the same recommendation can arise
from slightly different macroeconomic models with different behavioral expectations
(Branch et al., 2009; De Grauwe, 2011; De Grauwe, 2012a; Kurz et al., 2013). In addition
to these theoretical findings, we present empirical evidence from a laboratory experiment
leading to the same policy recommendation. We are aware that many macroeconomists are
still skeptical about the idea that one can learn about macroeconomic behavior by
conducting laboratory experiments (with small group sizes). However, while one cannot
mirror a completely macroeconomy with all its decisions in the laboratory, it is possible
to shed light on some specific macroeconomic questions. Our experiment is designed such
that it abstracts from everything except for the feedback mechanism from expectations to
realizations (which is altered by a one-parameter change). All decisions made by agents in
the economy are computerized and correspond fully to the underlying macroeconomic model
except for the forecasting of future variables. If such forecasts in the laboratory are
formed in similar ways as forecasts in the outside world, the results from the laboratory
experiment help to understand macroeconomic behavior. There is indeed recent evidence that
students’ forecasts in the laboratory have very similar characteristics to forecasts in
the outside world (Cornand and Hubert, 2018) supporting the external validity of
macroeconomic learning-to-forecast experiments.


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<ART>Multi-product firms at home and away: Cost- versus quality-based competence
===========================================================================

Authors: Carsten Eckel, Leonardo Iacovone, Beata Javorcik, J. Peter Neary
DOI: 10.1016/j.jinteco.2014.12.012
Year: 2015  |  Pages: 216-232
ASJC codes: 2002, 2003
Keywords: Flexible manufacturing, Investment in product and brand quality, Multi-product firms, Quality competition

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We develop a new model of multi-product firms which invest to improve the perceived quality of both their individual products and their brand. Because of flexible manufacturing, products closer to firms' core competence have lower costs, so firms produce more of them, and also have higher incentives to invest in their quality. These two effects have opposite implications for the profile of prices. Mexican data provide robust confirmation of the model's key prediction: firms in differentiated-good sectors exhibit quality-based competence (prices fall with distance from core competence), but export sales of firms in non-differentiated-good sectors exhibit the opposite pattern.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

What makes a successful exporting firm? This question has attracted much interest from
policy makers, keen to design effective export promotion programs, and from academics,
keen to understand the implications of globalization for economic growth. Two answers have
been proposed. The first focuses on firm productivity. Studies by Clerides et al. (1998)
and Bernard and Jensen (1999), among others, have found that firms self-select into export
markets on the basis of their successful performance at home. This evidence inspired the
theoretical work by Melitz (2003) where only the most productive firms find it worthwhile
to cover the extra costs of exporting. The second answer focuses on product quality. A
growing body of work has provided evidence that successful exporters charge higher prices
on average, suggesting that quality matters.1 This study integrates these two views and
shows both theoretically and empirically that firms may choose to compete on the basis of
either cost or quality depending on the characteristics of the products they sell and the
markets in which they operate.2 Unlike other studies which have compared the behavior of
different firms, and emphasized the between-firm extensive margin, we focus on the
portfolio of products sold by multi-product firms, and highlight what Eckel and Neary
(2010) call the “intra-firm extensive margin”. Our theoretical innovation is to construct
a model of multi-product firms in which the quality of goods is determined endogenously by
the firms' profit-maximizing decisions. Because of flexible manufacturing, products closer
to a firm's core competence have lower costs. As a result, firms produce more of those
products, but they also have higher margins on them, and therefore higher incentives to
invest in their quality. These two effects have opposite implications for the profile of
prices and, depending on which effect dominates, the model implies one of two possible
configurations which we call “cost-based” and “quality-based” competence, respectively.
The former corresponds to the case where a firm's core products are sold at lower prices,
in order to induce consumers to buy more of them. In the words of Jack Cohen, founder of
the UK supermarket chain Tesco, firms “pile 'em high and sell 'em cheap”. As a result, the
profile of prices across a firm's products is inversely correlated with its profile of
sales. By contrast, quality-based competence corresponds to the case where the dominant
effect comes from firms' investing more in enhancing the quality of their core products.
As a result, these products command higher prices, and so the profile of prices across a
firm's products is positively correlated with its profile of sales. Our model not only
allows for different profiles of prices but also makes predictions about which kinds of
goods should exhibit which profile. In particular, it predicts that a higher level of
product differentiation encourages firms to invest relatively more in the quality of
individual varieties than in the quality of their overall brand. As a result, quality-
based competence should be more in evidence in sectors where products are more
differentiated. We test this prediction using a rich Mexican data set already used by
Iacovone and Javorcik (2007, 2010). Most previous empirical studies of multi-product firms
at plant level have been constrained to use data on export sales only, or to combine
export and production data at different levels of disaggregation.3 By contrast, a unique
characteristic of our data is that it provides consistently disaggregated information on
both the home and export sales of all goods produced by a large representative sample of
manufacturing establishments.4 As we show, the Mexican data provide robust confirmation of
the model's key prediction: comparing price profiles with sales profiles, we find that
firms in differentiated-good sectors exhibit quality-based competence to a much greater
extent than firms in non-differentiated-good sectors, both at home and abroad. The
contrast is particularly striking in export markets, where Mexican producers in non-
differentiated-good sectors engage in cost-rather than quality-based competence. Our
results are robust to focusing attention on a variety of subsamples, including only those
products sold both at home and abroad, only those plants which sell on the home market and
also select into exporting, and only single-plant firms. Our paper builds on and extends
the existing literature on multi-product firms in international trade. While there already
existed a large literature on multi-product firms in the theory of industrial
organization, our model is one of a number of recent trade models which is more applicable
to the kinds of large-scale firm-level data sets which are increasingly becoming
available.5 Within this latter tradition, existing models impose one or other profile of a
firm's prices by assumption. One class of models assumes that products are symmetric on
both the demand and supply sides, with the motivation for producing a range of products
coming from economies of scope. As a result, all products sell in the same amount and at
the same price6. A different approach, pioneered by Bernard et al. (2010, 2011),
emphasizes asymmetries between products on the demand side due to exogenous stochastic
factors. Before they decide to enter, firms draw their overall level of productivity and
also a set of product-market-specific demand shocks. The latter determine the firm's scale
and scope of sales in different markets, and imply that its price and output profiles are
always positively correlated. By contrast, Eckel and Neary (2010) develop a model that
emphasizes asymmetries between products on the cost side and implies that price and output
profiles are always negatively correlated.7 The present paper integrates these demand and
cost approaches in an endogenous way. We extend the “flexible manufacturing” approach of
Eckel and Neary (2010) by allowing costs to affect the profile of investment in quality
across different varieties, and develop a model which is more in line with recent work on
models of heterogeneous firms that engage in process R&D: see, for example, Bustos (2011)
and Lileeva and Trefler (2010) on single-product firms, and Dhingra (2013) on multi-
product firms. It is even more closely related to those papers which allow for endogenous
investment in quality, such as Antoniades (2009) and Kugler and Verhoogen (2012),
including the view that quality is really perceived quality, which may be market-specific,
so investment in quality includes spending on marketing as in Arkolakis (2010). All this
work has so far focused on single-product firms only. Our specification is we believe the
first to incorporate investment in quality into a model of multi-product firms, combining
insights from extensive literatures in both industrial organization and marketing science.
From the former, especially Stigler and Becker (1977), we take the view that firms invest
in perceived quality through advertising, which enters the utility function directly in a
way that is complementary to consumption itself. From the latter, notably Jacoby et al.
(1971), Boush et al. (1987), and Aaker and Keller (1990), we take the view that consumers
of multi-product firms are affected both by product-specific marketing and by advertising
of a firm's overall brand, and that the relative effectiveness of the former is greater
when products are more differentiated. This brief review of the literature on multi-
product firms highlights our main interest: how the theoretical models differ in the way
they model the demand for and the decision to supply multiple products. The models also
differ in other ways which are of less interest in the present application. One type of
difference is in the assumptions made about market structure. In particular, most recent
models assume that markets can be characterized by monopolistic competition, in which
firms produce a large number of products but are themselves infinitesimal relative to the
size of the overall market.8 By contrast, Eckel and Neary (2010) assume in their core
model that markets are oligopolistic. In this paper, we know little about the market
environment facing individual firms: we do not know with which other Mexican plants in the
sample they compete directly, and we have no information at all on their foreign
competitors. Hence we prefer to remain agnostic on this issue, where possible deriving
predictions which will hold at the level of individual firms irrespective of the market
structure in which they operate. A further dimension of difference concerns the level of
analysis, whether partial or general equilibrium. Some of the trade theory papers,
including Eckel and Neary (2010), highlight general-equilibrium adjustments working
through factor markets as an important channel of transmission of external shocks.
However, with the data set we use, it is not possible to ascertain how factor prices are
affected by general-equilibrium adjustments to changes in trade policy. Hence, we
concentrate on testing implications of the model in partial equilibrium. Section 2 of the
paper presents the model and shows how differences in technology, tastes and market
characteristics determine whether a multi-product firm exhibits cost-based or quality-
based competence. Section 3 describes the data and explores the extent to which they
confirm our theoretical predictions. Finally, Section 4 summarizes our results and
presents some concluding remarks. The Appendix supplements and extends the theoretical
results of Section 2, and in particular shows that they extend to a Cournot oligopolistic
market with heterogeneous firms.

<h>THE MODEL</h>
---------

As already explained, the paper extends the flexible-manufacturing model of Eckel and
Neary (2010) to allow for the interaction of quality and cost differences between the
varieties produced by a multi-product firm. To simplify ideas and notation, we focus in
the text on a single monopoly firm, but, as we show in Appendix B, all the results extend
to a heterogeneous-firm industry in which firms engage in Cournot competition. Section 2.1
introduces our specification of preferences, while Section 2.2 briefly reviews the earlier
model, which allowed for cost-based competence only, showing how a firm chooses its
product range, its total sales, and their distribution across varieties in a single
market. Section 2.3 explores the additional complications which quality-based competence
introduce and derives our main theoretical result, and Section 2.4 considers the model's
comparative static properties.

<hs>  Preferences for quantity and quality</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As discussed in the introduction, we remain agnostic in the paper about whether this sub-
utility function is embedded in a general- or partial-equilibrium model: our analysis is
compatible with both approaches. All we need is to assume that the marginal utility of
income can be set equal to one. This is ensured if the sub-utility function (1) is part of
a quasi-linear upper-tier utility function, with all income effects concentrated on the
“numéraire” good. Alternatively, as in Eckel and Neary (2010), (1) can be one of a mass of
sub-utility functions without an outside good, with the marginal utility of income set
equal to unity by choice of numéraire. In either case, Eq. (1) is only one of the many
sub-utility functions, corresponding to separable preferences for different groups of
products. In our empirical work we will allow for the possibility that key parameters, and
especially the product differentiation parameter e, may vary across markets and countries.
To economize on notation we do not make this explicit in Eq. (1).

<hs>  Cost-based competence</hs>
  ~~~~~~~~~~~~~~~~~~~~~

Consider next the technology and behavior of the firm in a single market, which is
segmented from the other markets in which the firm operates. The firm's objective is to
maximize profits by choosing both the scale and scope of production, as well as choosing
how much to invest in enhancing the quality of individual varieties and of its overall
brand. We begin by abstracting from the quality dimension in this sub-section, and
recapping the results of Eckel and Neary (2010) for the case where the firm's competence
derives from differences between varieties in production costs only. This is most easily
done by setting β equal to zero in Eq. (1), so utility does not depend on quality. Though
it is convenient to make explicit the variety-specific intercepts a(i) in all equations,
we do not consider the implications of differences between them until the next sub-
section.

<hs>  Quality-based competence</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~

Our modeling of preferences and investment in perceived quality draws on previous work in
both industrial organization and marketing science. Our assumption that both perceived
quality and the physical quantities of goods consumed enter the utility function is
consistent with the “complementary view” of advertising in the industrial organization
literature. This can be traced back to Stigler and Becker (1977, p. 84), who argue that
“utility depends not only on the quantity of the good but also the consumer's knowledge of
its true or alleged properties” and that “the knowledge, whether real or fancied, is
produced by the advertising of producers”. Bagwell (2007, p. 1720) adds that a “consumer
may value ‘social prestige’, and advertising by a firm may be an input that contributes
towards the prestige that is enjoyed when the firm's product is consumed.” By
distinguishing between product-specific investments in perceived quality and investments
in the quality of a firm's (umbrella) brand, we extend this framework to a multi-product
setting. This result has been derived the case of a single monopoly firm, but it is
independent of the extent of competition which the firm faces. We show formally in the
Appendix that it continues to hold in a heterogeneous-firms Cournot oligopoly market, but
the intuition is straightforward. With all goods symmetrically differentiated, firms
compete against each other only at the level of total output, not at the level of
individual varieties. Changes in the extent of inter-firm competition affect the scale and
scope of production as well as the level of investment in quality, but do not influence
the within-firm profile of prices across products, which is the focus of our empirical
analysis.

<hs>  Comparative statics</hs>
  ~~~~~~~~~~~~~~~~~~~

The predictions of the model for the shape of the firm's equilibrium price profile given
in Proposition 1 are the ones that we take to the data in the next section. It is also of
interest to explore the comparative statics properties of the model. Here we note the
effects of exogenous shocks on the scale and scope of a single monopoly firm, while in the
Appendix we show that our results generalize to the case of a group of firms engaged in
Cournot competition.

<h>EMPIRICS</h>
--------

Our theoretical model makes a number of novel predictions about the behavior of multi-
product firms. One of these in particular is unique to our model, has both theoretical and
policy interest, and lends itself to empirical testing with our data. This is the
prediction from Corollary 1 that the profile of prices across the different goods produced
by a multi-product firm is more likely to be positively correlated with the corresponding
profile of outputs, thus exhibiting what we have called quality-based competence, when
products are more differentiated. In the remainder of the paper we subject this prediction
to empirical testing. We first describe the data and document the profiles of sales across
firms' products which it exhibits; then we explain how we operationalize the prediction
about price profiles; subsequent sub-sections present the results of testing it and
consider various robustness checks.

<hs>  The data</hs>
  ~~~~~~~~

We begin by reviewing the data set.21 A unique characteristic of our data is the
availability of plant-product level information on the value and the quantity of sales for
both domestic and export markets. Our data source is the Encuesta Industrial Mensual (EIM)
administered by the Instituto Nacional de Estadstica Geografa e Informática (INEGI) in
Mexico. The EIM is a monthly survey conducted to monitor short-term trends and dynamics in
the manufacturing sector. As we are not primarily interested in short-term fluctuations,
we aggregate the monthly EIM data into annual observations. The survey covers about 85% of
Mexican industrial output, with the exception of “maquiladoras”.22 It includes information
on 3183 unique products produced by over 6000 plants.23 Plants are asked to report both
values and quantities of total production, total sales, and export sales for each product
produced, making the data set particularly valuable for our purposes. Note that the unit
of observation is the plant rather than the firm: we return to this issue in our
robustness checks below. Products in the survey are grouped into 205 clases, or activity
classes, corresponding to the 6-digit level CMAP (Mexican System of Classification for
Productive Activities) classification. Each clase contains a list of possible products,
which was developed in 1993 and remained unchanged during the entire period under
observation. The classification of products is similar in level of detail to the 6-digit
international Harmonized System classification, though with differences that reflect
special features of the structure of Mexican industrial production.24 Table 2 shows that
the number of plants in the sample varies from 6291 in 1994 to 4424 in 2004. Between 1579
and 2137 plants were engaged in exporting.25 The decline in the number of establishments
during the period under analysis is due to exit.26 In our empirical analysis, consistent
with our theoretical model, we refer to each plant-product combination as a “variety”. The
number of varieties sold ranges from 19,154 in 1994 to 12,887 in 2004, while the number of
varieties exported rose from 2844 in 1994 to 3118 in 2004, reaching a peak of 4193 in
1998.

<hs>  Sales profiles</hs>
  ~~~~~~~~~~~~~~

As a first step in exploring the properties of the data through the lens of our
theoretical model, we considered the patterns of sales across the varieties produced by
different plants in our sample. (Details are given in a background paper: Eckel et al.
(2009)). The results were consistent with the model presented in Section 2, and also
broadly in line with empirical patterns found in other recent studies of multi-product
firms.27 In particular, the data show that exporting plants are larger, and that larger
plants produce more products. The vast majority of plants sell more products at home, and
most exported products are also sold at home. Finally, the profile of sales across
products is highly non-uniform, with a broadly similar ranking of products by sales in the
home and foreign markets.

<hs>  Empirical strategy</hs>
  ~~~~~~~~~~~~~~~~~~

We wish to use estimates of Eq. (21) to test the prediction of Proposition 1 that a higher
degree of product differentiation should make firms more likely to exhibit a price profile
that reflects quality-based rather than cost-based competence. To implement this test, we
need independent observations on the degree of product differentiation, and for this
purpose we make use of the classification developed by Rauch (1999). He grouped goods by
the Standard International Trade Classification (SITC), Revision 2, four-digit
classification into three categories, “differentiated,” “traded on organized exchanges,”
or “reference priced.” We combine the latter two into a catch-all “non-differentiated”
category, and follow many authors in adopting the so-called “liberal” classification,
which maximizes the number of goods classified as non-differentiated.31 To implement this
classification with our Mexican data, we had to make a concordance between the clases in
our data and the SITC system. Fortunately, this was possible without too much
arbitrariness.32 We are thus able to explore how the relationship between the price and
sales profiles of multi-product firms varies with the degree of product differentiation.

<hs>  Results for price profiles at home and away</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Table 3 gives the results of estimating Eq. (21) over different subsets of the data on all
plant/product/year observations for which the plant in question sells at least five
products. Each column gives the results of regressing the corresponding price on product-
year and plant-year fixed effects and on dummy variables for the highest to fourth-highest
selling products. Thus, in the first equation, the coefficient 0.091 gives the estimated
price premium on the top-selling product in the home market relative to the average price
on the excluded category of all products ranked fifth or lower in home sales. This
coefficient is highly significant, indicating that, on average, the highest-selling
product from each plant commands a price premium of 9.1% (i.e., exp (0.091)-1). This
provides strong evidence of quality-based competence, in the sense in which we have used
the term in our theoretical model. The other coefficients in this equation are also highly
significant, and fall steadily in size, again confirming a pattern of quality-based
competence. The fourth equation in the table shows that export sales exhibit a similar
pattern on average, with the coefficient on the dummy variable for the top-selling product
equal to 0.162 and highly significant, the coefficients on the next two not significantly
different from that of the top-selling product, and all three significantly greater than
the last coefficient, for the top fourth-selling product. The most interesting feature of
the table is the pattern of the estimated coefficients when we disaggregate by type of
product and by destination. Looking first at the second and third equations, both
differentiated and non-differentiated products sold at home exhibit the same pattern of
quality-based competition. However, each coefficient for differentiated products is
significantly greater than the corresponding coefficient for non-differentiated ones,
exactly as our theory predicts.33 This difference between the two categories of products
is repeated but to an even more striking extent in the export market, as the fifth and
sixth equations show. The top three coefficients for differentiated exports are all highly
significant and significantly larger than in the home market, implying even higher price
premia for the top-selling products in this category. By contrast, the coefficients on the
top four non-differentiated export products are all negative, implying that these products
exhibit cost-based rather than quality-based competence. So far we have only considered
the subset of firms selling five or more products. Tables 4–7 extend the analysis to
observations in which the same plant sold at least two, three or four products in the one
year. In each equation the residual category is all products with ranks lower than the
lowest-ranking dummy variable included, and the final equation is repeated for reference
from Table 3. The advantage of focusing on plants that export fewer than five products is
a considerable increase in degrees of freedom, and the results are qualitatively similar
to those in Table 3. Tables 4 and 5 confirm that the pattern of quality-based competition
which Table 3 showed for plants selling five or more products on the home market also
applies to plants selling fewer products. For differentiated products, Table 4 shows that
the implied price premium for the top product ranges from 4.1% when all plants producing
two or more products are included, to 11.5% when only those producing five or more are
included. In Table 5 the corresponding figures are 3.9% and 3.1%, showing once again that
non-differentiated products exhibit significantly less quality-based competition than
differentiated ones, as our theory predicts. Also of considerable interest is that the
pattern of prices falling with a product's rank which was found in Table 3 continues to
hold for the larger samples of plants selling fewer products. Not only are most
coefficients of the dummy variables for second- and lower-ranking products in these
equations significantly different from zero, but there is a clear and in many cases
significant downward trend in the coefficients in each column. We can thus conclude that
there is strong evidence that prices fall with a product's distance from a plant's core
competence, so the price and production profiles are negatively correlated, implying that
on average the firms in our sample compete on the basis of quality-based competence on the
home market. Tables 6 and 7 show that export sales behave even more differently depending
on the degree of product differentiation. Consider first Table 6, which shows that the
price profile of exports in differentiated sectors is qualitatively similar to that at
home. The evidence for a monotonically decreasing profile is less strong in the case of
plants producing five or more products, although this may be due to the smaller number of
observations in this sub-sample, and in any case the top three products command a
significant price premium over products ranked fifth or lower. Moreover, the quantitative
magnitude of the effects is much higher than in Table 4: the price premium for the top
product ranges from 8.5% when all plants producing two or more products are included, to
22.8% when only those producing five or more are included, compared with 4.1% and 11.5%
respectively in Table 4. By contrast, Table 7 tells a very different story for exports of
non-differentiated products. Not a single coefficient in this table is significantly
positive, most are negative, and the overall pattern is one of increasing coefficients as
we move down each column. Unlike Tables 4, 5 and 6, this provides strong evidence against
quality-based competence, and suggestive evidence in favour of cost-based competence for
exports of non-differentiated products. Though not as overwhelmingly significant as the
results for differentiated products, the results imply that the two groups of products
behave very differently, and exactly in the way predicted by Proposition 1. For
differentiated exports, prices fall with their distance from the plant's core competence,
suggesting that Mexican exporters in these sectors compete on the basis of quality. By
contrast, for non-differentiated exports, prices tend to rise with their distance from the
plant's core competence, suggesting that competition in such sectors is on the basis of
cost rather than quality, exactly as our theory suggests. Overall, these four tables
confirm that the coefficient pattern summarized in Eq. (22) continues to hold when we
consider plants that sell up to five or more products.

<hs>  Robustness checks</hs>
  ~~~~~~~~~~~~~~~~~

A possible concern with the results so far is that the sample sizes are very different in
different tables, with more products produced for the home market than for exports. This
is perfectly consistent with our model which predicts that higher costs of accessing a
foreign market will reduce the range of products sold there. Nevertheless it might suggest
a concern that the regularities we have found in our data reflect behavior very different
from that predicted by our model; for example, that plants sell different products in the
home and foreign markets, or that plants which select into exporting are very different
from those that sell only on the home market. To address these concerns we reestimate our
price profile equations first for those products that are sold on both markets, and next
for the home sales of exporting plants. We also present results for various subsets of the
data, including firms with only a single plant and plants that are either domestically- or
foreign-owned. Table 8 addresses the issue of different sample sizes directly by
reestimating the equations for only those observations on products that are both exported
and sold at home, so the numbers of observations are the same at home and abroad. It can
be seen that the conclusions drawn from the earlier tables survive this robustness check.
There is clear evidence of quality-based competition in differentiated products in both
home and foreign markets, and this contrasts with the absence of a pattern in the
coefficients for non-differentiated products. Even in the latter case, the size and sign
of the coefficients, though not their significance, are consistent with those from the
larger samples in Table 3. We can conclude that the evidence from this smaller sample is
less overwhelmingly in support of different behavior by non-differentiated product plants
at home and away; but that the evidence for a difference between behavior by plants in
differentiated and non-differentiated sectors remains strong in both domestic and export
markets. Table 9 addresses the question of whether plants that select into exporting
behave differently on the home market. It gives results for home sales by export plants in
both differentiated and non-differentiated clases, and it is clear that the two behave
very similarly to the corresponding samples of all plants selling on the home market, as
in Tables 4 and 5. Once again, home sales of differentiated products exhibit quality-based
competence, while those of non-differentiated products do not. Bearing in mind that the
plants in Table 9 are identical to those whose exporting behavior is shown in Tables 6 and
7, our earlier conclusions are reinforced. Exporting plants in differentiated sectors
exhibit quality-based competence in the home market, whereas those in non-differentiated
sectors do not, so the very different behavior of exporters in non-differentiated sectors
shown in Table 7 does not reflect any differential selection process of plants into
exporting. A different robustness check addresses the concern that our theory was
developed for multi-product firms, whereas our data consist of observations on multi-
product plants. Treating plants as the unit of observation ignores the interdependence of
decision-making within multi-plant firms. To deal with this problem empirically we would
ideally like to have data on the ownership patterns of plants in all years. Unfortunately,
we can only identify which plants were owned by the same firm in the penultimate year of
our sample, 2003. We therefore adopt the following strategy. We retain in the sample only
those plants which were single-plant firms in 2003, and consider their sales and price
profiles in all years. This risks including some observations on plants which did not
correspond to single-plant firms either in 2004 because of mergers and acquisitions, or in
years prior to 2003 because of divestitures. However, the number of such cases is likely
to be small, and this strategy seems preferable to losing many more degrees of freedom by
focusing on single-plant firms in 2003 only.34 Table 10 gives the results of this
robustness check, for single-plant firms selling at least five products. The evidence for
quality-based competence remains very strong for both categories of home sales and for
differentiated exports. For these three categories, most coefficients are highly
significant, implying that products closer to the core sell for higher prices than the
non-core products in the default category of each equation. As for exports of non-
differentiated products, the evidence for cost-based competence is weaker than in earlier
tables, though the hypothesis that these sales exhibit quality-based competence is
strongly rejected. We can conclude that our earlier results are robust to excluding plants
owned by multi-plant firms in 2003. A final concern we address is whether our
specification is more applicable to Mexican-owned plants or to foreign-owned ones. On the
one hand, we would expect the decisions of foreign-owned Mexican plants to be taken as
part of the global operations of their parent multinational companies rather than on a
stand-alone basis, at least for sales in their export markets, and perhaps in their home
market too. This would suggest that the considerations we have highlighted in our
theoretical model should apply more to Mexican-owned plants. On the other hand, we would
expect multinational companies to have stronger world brands and so to exhibit more
quality-based competence in all markets. It seems appropriate therefore to check whether
the results hold when we consider the two groups of plants separately. Tables 11 and 12
show that the pattern summarized in Eq. (22) continues to hold for both groups of plants,
though there are interesting differences between them. First, domestically-owned plants
have almost flat price profiles in export markets, showing that even in differentiated
sectors these plants do not compete on quality, though the results suggest that non-
differentiated exports come closer to exhibiting cost-based competence. Second, foreign-
owned plants compete strongly on quality even in the home market, as we might expect,
leveraging their superior brands even in non-differentiated sectors. But they too compete
more on cost in export non-differentiated sectors, showing that their exports of these
goods do not command quality premia. Overall, the broad pattern from previous tables is
confirmed for both groups of plants, and is most pronounced for foreign-owned plants.

<h>CONCLUSION</h>
----------

This paper has developed a new model of multi-product production in which firms invest to
improve the quality of their products as well as the quality of their overall brand. It is
thus the first to integrate two important strands of recent work on the behavior of firms
in international markets. On the one hand, the growing evidence that many firms, and
especially most large exporters, are multi-product, has inspired theoretical and empirical
work which focuses on the “intra-firm extensive margin”, changes in the range of products
produced by firms, distinct from the inter-firm extensive margin which has attracted so
much attention in the literature on heterogeneous single-product firms. On the other hand,
an increasing number of authors have suggested that successful firms in international
markets compete on the basis of superior quality rather than superior productivity. Our
model integrates these two strands in a tractable framework. Crucially, it endogenizes
both the choice of product range and the choice of quality, or more specifically, the
choice of investment in quality, thus allowing a range of issues to be explored which have
so far been little studied. The model has interesting implications for the manner in which
firms compete in international markets. In particular, it throws light on the question of
whether productivity or quality is the key to successful export performance, and suggests
a way of reconciling these two views. Because of flexible manufacturing, firms produce
more of products closer to their core competence. They also have incentives to invest more
in the quality of those goods. These two effects have opposite implications for the
profile of prices. On the one hand, to the extent that consumers view all products as
symmetrically differentiated substitutes for each other, firms can only sell more of their
core products by charging lower prices for them. Hence, the direct effect of lower
production costs for core products is that firms “pile 'em high and sell 'em cheap,”
implying that the profiles of prices and sales should be negatively correlated, an outcome
we call “cost-based competence”. On the other hand, firms face stronger incentives to
invest in raising the perceived quality of their core products, since these are the
products with the highest mark-ups. Even though investment in the quality of an individual
product is subject to diminishing returns, this implies that firms will invest more in the
quality of their core products, so raising the price which consumers are willing to pay
for them. This indirect effect of lower production costs for core products implies that
the profiles of prices and sales should be positively correlated, an outcome we call
“quality-based competence”. We show that both these outcomes are possible in our model,
and that which of them prevails depends on a number of exogenous factors. In particular,
the greater the degree of product differentiation, the more the firm faces differential
incentives to invest in the quality of different products, and so the more likely is the
indirect effect to dominate, giving rise to quality-based competence. We prove these
results in the text for the case of a single multi-product firm, and show in the Appendix
that they also hold in an oligopolistic model with heterogeneous firms. This last
prediction is the one we explore empirically, drawing on a unique data set on Mexican
plants already used by Iacovone and Javorcik (2007, 2010). A great advantage of this data
set is that it gives detailed information on both home and foreign sales at the same level
of disaggregation, allowing us to test theoretical predictions about their relative
profiles. Our findings show that a two-way distinction is crucial: between home sales and
exports on the one hand, and between differentiated and non-differentiated products on the
other. In the domestic market, we find that both differentiated and non-differentiated
products exhibit quality-based competence, with prices falling as sales value falls.
However, this pattern is significantly more pronounced for differentiated products,
exactly as our theory predicts. The same holds true in the export market, where the
difference in price behavior between the two groups of products is considerably greater:
plants in differentiated-product sectors exhibit quality-based competence in export
markets, but those in non-differentiated-good sectors exhibit cost-based competence, with
core-competence products selling for significantly lower prices on average. These results
turn out to be robust to a slew of alternative ways of grouping our data. We find very
similar results whether we consider all products or only those which are sold in both home
and foreign markets; and whether we consider all plants active in either market or only
those active in both. They also hold when we consider only the sub-sample of single-plant
firms: confirmation that our theory, which was developed for firms, helps in understanding
behavior at plant level too. Finally, the patterns we have found are exhibited by both
home-owned and foreign-owned plants. We can conclude that, for this data set, quality-
based competence is dominant for firms in differentiated-good sectors, but not for the
export sales of firms in non-differentiated-good sectors. Turning to policy, a full
consideration of the costs and benefits of different export-promotion strategies is beyond
the scope of this paper. Nevertheless, our results are suggestive. Export-promotion
policies take a variety of forms, and in the light of our results we can distinguish
between those that focus on cost and those that focus on quality. The former type of
intervention includes measures to stimulate investment in cost-saving technologies and
worker training. The latter type of intervention includes marketing campaigns to stress
the advantages of national products, and reductions in the costs of quality certifications
(e.g. ISO 9000 or 14000) to improve the producer's image. Without further research, it
would be premature to suggest that, in the light of our findings, export-promotion efforts
in middle-income countries such as Mexico should focus on helping producers to lower
production costs in non-differentiated-good sectors and on improving perceived product
quality in differentiated-good sectors. Nevertheless, our findings that Mexican firms
compete in foreign markets on either cost or quality, depending on whether they operate in
relatively homogeneous or relatively differentiated-good sectors, suggest that a “one-
size-fits-all” policy may not be the most effective way of promoting exports. Our findings
also have broader implications for the nature of competition in international markets. Our
data set shows that within-firm product heterogeneity is not just a rich-country
phenomenon, but is also important in at least one middle-income country. Moreover, the
evidence we present suggests that only firms in differentiated-product sectors compete in
export markets on quality. This has a key implication for understanding how firms compete
successfully abroad. While previous studies have shown that all exporters have a
productivity premium, our results suggest that those in differentiated-product sectors
have a quality premium too, whereas those producing non-differentiated goods behave
differently at home and away, competing less on quality and more on price in their export
markets.


<h>REFERENCES</h>
----------

  [2] Paul Allanson, Catia Montagna. Multiproduct firms and market structure: An explorative application to the product life cycle. doi:10.1016/j.ijindorg.2005.02.001
  [3] Costas Arkolakis. Market penetration costs and the new consumers margin in international trade. doi:10.1086/657949
  [4] Kyle Bagwell. Chapter 28 The Economic Analysis of Advertising. doi:10.1016/S1573-448X(06)03028-7
  [5] Andrew B. Bernard, J. Bradford Jensen. Exceptional exporter performance: Cause, effect, or both?. doi:10.1016/S0022-1996(98)00027-0
  [6] Andrew B. Bernard, Stephen J. Redding, Peter K. Schott. Multiple-product firms and product switching. doi:10.1257/aer.100.1.70
  [7] Andrew B. Bernard, Stephen J. Redding, Peter K. Schott. Multiproduct firms and trade liberalization. doi:10.1093/qje/qjr021
  [8] Unknown. Affect generalization to similar and dissimilar brand extensions; consumer behavior seminar. doi:10.1002/mar.4220040306
  [9] Paula Bustos. Trade liberalization, exports, and technology upgrading: Evidence on the impact of MERCOSUR on argentinian firms. doi:10.1257/aer.101.1.304
  [10] Sofronis K. Clerides, Saul Lach, James R. Tybout. Is learning by exporting important? Micro-dynamic evidence from Colombia, Mexico, and Morocco. doi:10.1162/003355398555784
  [11] Swati Dhingra. Trading away wide brands for cheap brands. doi:10.1257/aer.103.6.2554
  [13] Carsten Eckel, Peter P. Neary. Multi-product firms and flexible manufacturing in the global economy. doi:10.1111/j.1467-937X.2009.00573.x
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  [18] Maurice Kugler, Eric Verhoogen. Prices, plant size, and product quality. doi:10.1093/restud/rdr021
  [19] Dermot Leahy, J. Peter Neary. Public Policy Towards R&D in Oligopolistic Industries
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<ART>News-driven business cycles in small open economies
===================================================

Authors: Güneş Kamber, Konstantinos Theodoridis, Christoph Thoenissen
DOI: 10.1016/j.jinteco.2016.12.005
Year: 2017  |  Pages: 77-89
ASJC codes: 2002, 2003
Keywords: Business cycles, Financial frictions, News shocks, Open economy macroeconomics, VAR

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

The focus of this paper is on news-driven business cycles in small open economies. We make two significant contributions. First, we develop a small open economy model where the presence of financial frictions permits the replication of business cycle co-movements in response to news shocks. Second, we use VAR analysis to identify news shocks using data on four advanced small open economies. We find that expected shocks about the future Total Factor Productivity generate business cycle co-movements in output, hours, consumption and investment. We also find that news shocks are associated with countercyclical current account dynamics. Our findings are robust across a number of alternative identification schemes.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Does news about future Total Factor Productivity (TFP) generate business cycles in small
open economies? A long tradition in macroeconomics and some recent empirical evidence
suggests that news about the future might be an important driver of the business cycle.1
There has been a lot of recent interest in incorporating this idea into modern business
cycle models. One of the main challenges emerging from this literature is to develop
equilibrium business cycle models that replicate data-congruent macroeconomic co-movement
in response to news shocks.2 The emphasis in most of this literature, particularly on the
empirical side, is on the effect of news shocks in closed economies. In this paper, we
focus on the effect of news shocks in small open economies. We make two contributions.
First, we put forward a novel mechanism through which news about future TFP causes
business cycles. This mechanism is based on the presence of financial frictions.
Specifically, the model incorporates financial frictions à laJermann and Quadrini (2012)
into an otherwise canonical small open economy model. The financial friction in this model
arises because firms need to arrange a working capital loan prior to production taking
place. Access to finance is constrained by the firm's net wealth position. News shocks
interact with the financial friction by relaxing the borrowing constraint faced by firms.
This allows firms to increase their demand for labour, which raises output and investment
in anticipation of future increases in TFP. Greater investment and labour input today
creates the expectation of higher dividends in the future, thus raising the share price in
anticipation of future TFP. Our second contribution is to identify and analyse the effects
of news shock in a set of advanced small open economies. Specifically, we identify the
dynamic macroeconomic effects of news shocks in four developed small open economies:
Australia, Canada, New Zealand and the United Kingdom. The way news shocks are identified
in the data is informed by the theoretical impulse responses of the model. In particular,
our identification strategy, based on Beaudry et al. (2011b), imposes model consistent
restrictions on the path of TFP, share prices and consumption. For TFP, this implies that
news arrives not one, as is the convention in the literature, but two periods in advance.
We also impose a restriction that at the end of the news horizon, TFP actually increases
for a number of periods. Consistent with our model, we restrict share prices and
consumption to rise in response to news. We find consistent evidence that news shocks
generate business cycles. As in our theoretical model, a news shock leads to positive co-
movement between GDP, hours worked and investment as well as a counter-cyclical trade
balance. Our results are robust across a number of alternative identification schemes,
including an augmented Barsky and Sims (2011) identification.3 To our knowledge, this is
the first account of the effect of news shocks in advanced small open economies. The next
section puts our contribution into the context of the literature analysing news shocks. We
document the theoretical model and the transmission of the news shocks in Section 3 and 4.
Section 5 and 6 present data and our preferred shock identification mechanism. In Section
7 we present our empirical results and perform a number of robustness tests around our
baseline identification of news shocks. Further sensitivity analysis is reported in the
online appendix to this paper.

<h>LITERATURE AND MODEL CHOICE</h>
---------------------------

News shocks in a standard open economy real business cycle model do not generate news-
driven business or Pigou cycles. In this class of model, news about a future TFP
improvement creates a positive wealth effect that raises both household consumption and
leisure, thus reducing the supply of labour. In the absence of an actual increase in TFP,
labour demand remains unchanged and as a result output falls in response to news.
Jaimovich and Rebelo (2008, 2009) show that when preferences are such that the wealth
effect on labour is small, hours worked do not decline following a news shock. Eliminating
the wealth effect on hours is, however, not enough to generate an actual increase in
labour demand when an increase in TFP is anticipated but not yet realised. Jaimovich and
Rebelo (2009) show that in a closed economy setting, this can be achieved by a combination
of investment adjustment costs and variable capital utilisation. The presence of
investment adjustment costs causes firms to bring the anticipated increase in future
investment, associated with the increase in future TFP, forward into the current period.
In a closed economy model, the hump shaped response of investment causes current period
Tobin's q to fall, which in turn raises the rate at which firms utilise capital. The rise
in capital utilisation raises the marginal product and thus the demand for labour. This is
enough to generate new-driven business cycles. For a small open economy, the challenge of
generating news-driven business cycles is slightly different. With real interest rates
determined abroad, Tobin's q always rises following a news shock. As a result, adding
variable capital utilisation does not help generate business cycles in response to news
shocks. Jaimovich and Rebelo (2008) show that adding labour adjustment costs that penalise
large changes in labour input, will cause firms to bring forward into the current period
some of the expected future increase in labour demand.4 Our modelling approach relies not
on costly adjustment in the labour market, but on a simple form of financial friction to
increase the demand for labour following news about future TFP. This friction introduces a
wedge between the marginal product of labour and the real wage. Following Jermann and
Quadrini (2012), we assume that because of limited enforcement of financial contracts,
firms face an enforcement constraint on working capital loans. Because firms have to
borrow the wage bill, the ‘tightness' of the enforcement constraint creates a wedge
between the marginal product of labour and the real wage. In our model, good news about
future TFP relaxes the enforcement constraint and increases the demand for labour. The
intuition behind our results is similar to Pavlov and Weder (2013) who consider a model
with counter-cyclical mark-ups. In their model, mark-ups create a wedge between the
marginal product of labour and the real wage. A news shock that lowers the mark-up also
reduces the labour wedge, raising firms' labour demand. Related to our analysis is
Walentin (2012), who examines news shocks in a model with limited enforcement where firms
face a collateral constraint when securing external finance. As in our model, the arrival
of news relaxes the borrowing constraint and raises share prices, which leads to an
accelerator type effect on investment. The key difference between our approach and that of
Walentin (2012) is that in our model, the firm faces the enforcement constraint on working
capital, whereas in Walentin (2012), the loan is inter-temporal. Financial frictions
impact the business cycle via an accelerator type mechanism. This difference between our
approaches matters, because only in our case does the financial friction create the
aforementioned labour wedge that is helpful in generating a positive co-movement between
consumption and hours.5 The literature on news shocks to TFP can be seen as being part of
a wider literature on the transmission of total factor productivity shocks. Both news
shocks and highly persistent, but contemporaneous, shocks to TFP have an expectations as
well as a supply component. In the initial response to a news shock about TFP, the
transmission mechanism is dominated by the expectations component of the shock. In a
highly persistent shock to TFP, the initial transmission mechanism is affected by both the
expectations as well as the supply component. In many dimensions, news and highly
persistent shocks may be expected to have similar effects on the economy. In the context
of emerging market economies, Aguiar and Gopinath (2007) highlight the importance of
highly persistent TFP fluctuations that are akin to shocks to trend growth. These kinds of
shocks help explain the somewhat non-standard business cycle fluctuations of emerging
market economies. Even for developed economies with ‘standard’ international business
cycle characteristics, Corsetti et al. (2008a) show that highly persistent productivity
shocks can bring a fairly standard international real business cycle model much closer to
the data. In particular, the expectations component of highly persistent TFP shocks
creates a wealth effect which helps the model achieve plausible degrees of international
risk sharing. Corsetti et al. (2008b) and Corsetti et al. (2014) identify TFP shocks using
either long-run and sign restrictions, respectively. In both studies, the US real exchange
rate is found to appreciate following a persistent increase in US TFP. Importantly, this
real appreciation is not linked to the familiar Balassa-Samuelson mechanism, as both the
real exchange rate and the terms of trade are shown to appreciate. In a context of a
simple two-good international real business cycle model, this finding is reminiscent of a
response to a shock with a significant expectations component. Research by Nam and Wang
(2015) lends credence to this view. They use an identification method that divides TFP
shocks into a contemporaneous as well as an anticipated, or news, component. When
separating the expectations from the supply component of a TFP shock, the authors find
that for the US economy, anticipated TFP shocks are associated with a real appreciation,
whereas contemporaneous shocks are linked to a depreciation. Whereas the empirical
literature on the transmission mechanism of contemporaneous TFP shocks in open economies
is well advanced, the empirical literature on in the transmission mechanism of news shocks
in open economies, to which our paper is a contribution, is not. There are two notable
exceptions. The aforementioned Nam and Wang (2015), who focus exclusively on the US
economy and a recent paper by Fratzscher and Straub (2013). The latter authors use a
canonical two-country new Keynesian model in which news shocks are used to identify
changes in asset prices that are not related to current fundamentals. Related to our work,
they analyse asset price shocks in small open economies, including the four in our sample.
However, since the focus of their work is on asset price shocks, no effort is made to
properly identify news-driven business cycles. Indeed, their baseline model shows a
decline in investment following a news shock, and their empirical work does not report the
response of investment or employment. In contrast, we identify news shocks as shocks that
raise the share price as well as lead to a path of TFP that is consistent with news about
future total factor productivity. We use the thus identified shock to check whether news
shocks can be a candidate driver of the business cycle and generate business cycle
consistent co-movements among macroeconomic aggregates.

<h>A SIMPLE SMALL OPEN ECONOMY MODEL WITH FINANCIAL FRICTIONS</h>
----------------------------------------------------------

We extend the flexible price version of the model presented in Jermann and Quadrini (2012)
into a small open economy setting. To turn a closed economy real business cycle model into
a small open economy model requires only a few changes to be made to the structure of the
model. In an open economy, the savings of households do not have to equal the borrowing by
firms. The gap between savings and investment equals the current account balance. Unlike a
closed economy, the gross or pre-tax interest rate faced by households and firms is
exogenous in a small open economy setting. This rate is determined instead by the world
interest rate as well as a small risk premium to ensure a well defined steady state.6
Firms and households produce and consume a homogeneous good. This good is a perfect
substitute for output produced in the rest of the world. As a result, the terms of trade
defined as the price of imports relative to exports are constant. We make the one-good
assumption for two reasons. First, abstracting from terms of trade movements allows us to
focus more clearly on the role of financial frictions in the transmission of news shocks.
Second, for commodity producers such as Australia, Canada and New Zealand, assuming an
exogenous terms of trade is quite realistic, although this is probably not the case for
the UK. As in Jermann and Quadrini (2012), we introduce financial frictions into the
environment in which domestic firms are operating. The household sector, on the other
hand, faces a standard optimisation problem.

<h>NEWS ABOUT TOTAL FACTOR PRODUCTIVITY</h>
------------------------------------

In Figs. 1 to 2 we assess the contribution of financial frictions to the generation of
positive co-movement between consumption and hours worked in response to news shocks. To
do this, we compare our baseline model to a version where the dividend payout cost is set
to zero. This version of our model is similar to the model in Jaimovich and Rebelo (2008).
The calibration of our model follows Jermann and Quadrini (2012) for the financial
frictions part of the model, such that ξ = 0.162 and τ = 0.35. We set κ = 0.146, which
corresponds to the value in Jermann and Quadrini (2012). Sensitivity analysis shows that
in our baseline calibration with non-separable preferences, we get news-driven business
cycles for any positive value of κ. For separable preferences (when γ = 0.999), our model
generates news-driven business cycles for any value of κ greater than 0.09. Fig. 1
analyses the response of key macroeconomic aggregates to an increase in TFP that is
expected to occur in period t + 2 and announced in period t.8 In our baseline model, hours
worked and GDP both increase as soon as the news about future productivity becomes
available. Without financial frictions, the agent's preferences over consumption and
labour ensure that the wealth effect on hours worked is weak. However, given our value of
γ, the wealth effect is small, but not zero, and hence hours worked decline on impact.
Because the real interest rate stays largely constant in our small open economy model,
share prices rise with the announcement of news. The initial increase in consumption and
investment is greater than the response of output, leading to a deterioration of the trade
balance and a decline in the economy's net foreign asset position. Because of the way we
have closed the model using a small debt-elastic interest rate risk premium, ζ in Eq.
(19), the decline in the net foreign asset position raises the real interest rate faced by
households and firms and thus also affects the path of consumption and investment.
Following a positive news shock about TFP the term Δtφ′(dt) falls, which for a given
marginal product of labour raises the real wage. The rise in the real wage causes agents
to increase hours worked and thus output to rise. Once TFP increases, the firm's borrowing
constraint becomes more binding, Δt rises, due to more output needing to be financed in
advance of production. A feature of the Jermann and Quadrini (2012) model is that a
tightening of the borrowing constraint causes hours worked to decline. In the next
subsection, we analyse why the borrowing constraint is relaxed during the news period,
causing hours worked to rise.

<hs>  Intuition</hs>
  ~~~~~~~~~

As dividend payouts decline on impact and then recover, the discount factor falls. In
other words, the firm becomes less patient and thus faces a more binding borrowing
constraint. As a result, the firm's demand for labour declines. This mechanism explains
the observed decline in hours worked once the anticipated increase in TFP materialises in
Figs. 1 to 2. When the increase in TFP is anticipated, the firm finds it optimal to start
reducing the flow of dividends before TFP actually increases in order to finance increased
investment. Thus dividends start to decline as soon as the news about future TFP becomes
available. As in the case of an unanticipated increase in TFP, dividend adjustment costs
reduce the magnitude of the fall in dividend payouts and smooth the dynamics of dt. The
gradual fall in dividends affects the firm's stochastic discount factor via the dividend
adjustment cost function. When dividends are expected to fall over time, the firm's
discount factor rises, which makes the firm want to hold less debt. Therefore, the firm's
desire to gradually reduce dividend payments in order to expand investment and labour
input also leads to a de-leveraging of the firm. The combination of a higher expected
capital stock and lower inter temporal borrowing thus improves the firm's net asset
position, which in turn relaxes the intra-temporal borrowing constraint. The less binding
the constraint, the smaller Δt and the greater will be the firm's demand for labour (see
Eq. (6)). This mechanism explains the role of financial frictions in generating news-
driven business cycles in our model. Importantly, as we show in Fig. 2, this mechanism can
be strong enough to off-set the wealth effect on hours worked.

<hs>  Separable preferences</hs>
  ~~~~~~~~~~~~~~~~~~~~~

In this section, we examine whether the mechanism identified above is strong enough to
overcome the negative wealth effect on hours that one finds in models with separable
preferences over consumption and labour. The utility function put forward by Jaimovich and
Rebelo (2008) nests both non-separable (when γ is close to zero) and separable preferences
(when γ is close to unity) over consumption and labour. Fig. 2 shows the response to a
news shock when γ = 0.99 for an otherwise unchanged calibration. Even with largely
separable preferences, GDP and its components display typical business cycle behaviour,
with output, consumption and investment and hours all rising on impact. As in the non-
separable case, there is a reduction in labour demand once TFP actually increases. This is
because as output rises, so does the demand for intra-period finance, which in turn causes
the enforcement constraint to tighten.

<h>DATA</h>
----

Next, we estimate a VAR model using data on total factor productivity, stock prices and
five macroeconomic aggregates: output, consumption, investment, total hours worked and net
trade. Where applicable, our data is normalised by the relevant working age population.
For each country our data is from OECD and obtained via HAVER. Our sample period is mainly
dictated by data availability and covers 1989Q3 to 2011Q3. Our macroeconomic aggregates
and our measure of stock prices are constructed as follows: Output: log(GDP in millions of
chain linked domestic currency / working age population); Consumption: log(Private
consumption in millions of chain linked domestic currency / working age population);
Investment: log(Private non-residential fixed capital formation in millions of chain
linked domestic currency / working age population); Total hours: log(Employment in
thousands  × Hours worked per employee in total economy / working age population); Net
trade to GDP: (Export of goods and services in millions of chain linked domestic
currency/GDP in millions of chain linked domestic currency - Imports of goods and services
in millions of chain linked domestic currency/GDP in millions of chain linked domestic
currency); Stock prices: log(Stock prices / Consumer price index). We use the following
stock price series: ‘All Ordinaries' for Australia, S&P/TSX Composite index for Canada,
NZSX Mid Cap for New Zealand and the FTSE 100 for the UK.

<hs>  A measure of total factor productivity</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our method of constructing quarterly total factor productivity is based on Fernald (2014).
Basu et al. (2006) argue that because of sectoral heterogeneity in the marginal product of
factors, one should ideally measure TFP at the sectoral level and then aggregate across
sectors to derive an aggregate measure of TFP. Furthermore, unobserved variations in
factor utilisation must also be accounted for. They proxy the unobserved changes in
capital utilisation and labour effort by observed changes in hours worked per capita.
Whereas data on capital utilisation, hours worked, output and total labour force are
available for our sample of countries at quarterly frequency, we have to construct
quarterly data for effort and the capital stock. We follow Basu et al. (2006) and proxy
the change in effort by the change in average hours, det = ζdnt. To construct a quarterly
series of the capital stock, we use annual capital data from the OECD and transform it to
quarterly frequency using information on quarterly investment. Our approach consists of
allocating capital into each quarter proportionally to the investment on that particular
quarter. Consistently with the calibration of our model we set α to 0.3. The coefficient
that links changes in effort to hours worked, ζ is set to 1. We have experimented with
values between 0.1 and 10 and found that our results are robust provided ζ is non-zero.
Output, yt and total hours nt are defined as above. We construct a quarterly measure of
the capital stock using annual OECD data on ‘Productive capital stock’, and quarterly
investment. As defined above, investment is taken from the OECD's private non-residential
fixed capital formation series. For each quarter, we use the share of total investment
over the whole year occurring in this quarter in order to determine this quarter's change
in the total capital stock from this year to the next. Therefore, our constructed
quarterly capital stock is consistent with annual capital stock taken from the data. HAVER
supplies measures of capacity utilisation from a number of sources. For Australia, we use
the NAB Business Survey's measure of capacity utilisation, for Canada, we use the
‘Capacity Utilisation - total industry’ measure. For the UK, we use the Harmonized
Capacity Utilisation series and for New Zealand, we use capacity utilisation in
manufacturing and construction. All series are reported in percentages and divided by 100.

<hs>  Country-specific shocks</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

It is likely that TFP growth in small open economies has both a domestic as well as a
foreign component. To take account of this, we would ideally adjust our TFP series by a
measure of global TFP to allow us to isolate country-specific shocks to TFP. There is,
however, no obvious measure of world TFP available, hence we take the quarterly TFP series
by Fernald (2014), for the United States as a proxy.

<hs>  Stock prices and macroeconomic aggregates</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Stock prices are stock market indexes deflated by CPI for each country. Output and
consumption correspond to gross domestic product and private consumption in real prices,
respectively. Investment refers to private non-residential fixed capital formation in real
prices. Total hours for each country is constructed as a product of employment and hours
worked per employee. All macroeconomic aggregates are divided by the working age
population and are therefore expressed in per capita terms. Net trade is the the
difference between exports and imports of goods and services divided by output.

<h>THE TIME SERIES MODEL</h>
---------------------

The number of lags has been selected using information criteria (likelihood ratio test
statistic, final prediction error and Akaike's information criterion). All selection
criteria suggest that a VAR model with two lags is sufficient to capture the dynamic
properties of the macroeconomic data and this is the case for all countries. In order to
ensure that our inference is not driven by the selection of a particular lag length we
repeat the same analysis using lag choices (VAR(1), VAR(3) and VAR(4)) and the results
remain unchanged. For the estimation of the empirical model we rely on Bayesian inference
techniques as the large dimension of the observable vector (seven variables) and the small
time span of the macroeconomic data set cause Classical (OLS) estimates to be subject of
considerable uncertainty. In this case data is combined with prior information about the
reduced-form parameter vector in the form of a probability density function. Similar to
Beaudry et al. (2011b) we employ a flat Normal-Wishart conjugate prior that leads (after
being combined with the likelihood of the model) to a closed-form posterior probability
distribution for the VAR parameter vector9.

<hs>  Identification</hs>
  ~~~~~~~~~~~~~~

As in Beaudry et al. (2011b), we identify news TFP shock using a combination of zero type
and sign restrictions (Uhlig (2005)). To be precise, the TFP shock anticipated in t + h
period is identified by imposing zero restrictions on TFP for periods t, t + 1, …, t + h −
1 and sign restrictions on the responses of a set of variables in the system. Our
theoretical model suggests that news shocks are associated with positive co-movement
between macroeconomic aggregates and share prices as well as a counter-cyclical current
account. Based on this analysis, we impose that stock prices and consumption increase
after a positive news about future TFP. Our methodological strategy also enables us to
consider, in a VAR framework, news shocks beyond the first period (see, Barsky and Sims,
2011 and Beaudry et al., 2011b). That makes the VAR identified responses more comparable
to DSGE ones so the former responses can serve a useful device to either assess the
empirical predictions of the structural model about new shocks and/or to calibrate the
structural parameter vector in order for the DSGE model to replicate the responses
estimated in the data. This closes an important gap in the literature since so far the
comparison was achievable only for DSGE model with only one quarter anticipation period
(see Barsky and Sims, 2011, Kurmann and Otrok, 2013, Theodoridis and Zanetti, 2013 and
Pinter et al., 2013). In summary, the identification puts restrictions on the responses of
TFP, consumption and share prices. TFP is restricted to remain at zero for two quarters
and positive for the following two quarters. Consumption and share prices are restricted
to increase for four quarters following a positive news shock.

<hs>  Testing the identification technique on simulated model data</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In this section, we perform a Monte-Carlo experiment to compare the true impulse responses
to news shocks from the model presented in the previous section and those from a VAR using
our identification scheme. In order to estimate a VAR with as many variables as we have in
the empirical section, we introduce additional structural shocks into our model. In
addition to news about TFP, we also consider a standard contemporary TFP shock plus five
additional shocks. These are shocks to investment specific technology, financial shocks as
in Jermann and Quadrini (2012), government spending shocks and preference shocks and a
shock to the world real interest rate. The standard deviation of the two unanticipated
technology shocks (TFP and investment specific) is set to 0.75%, the standard deviation of
the news shock is set to 0.25% and the standard deviation of all other shocks is set to
0.15%. All shocks are assumed to have an AR(1) coefficient of 0.95. We generate 2000
artificial data sets from the model under our calibration corresponding to Fig. 1. The
sample size of each data set is 86, corresponding to the number of observations of the
actual data. Using the artificial data sets, we estimate VARs with TFP, output,
consumption, investment, total hours worked, net trade and stock prices as observables.
The VARs include two lags. We then identify impulse responses using the same
identification restriction employed in the empirical section. Fig. 3 displays the
theoretical and the range of estimated impulses responses over the Monte-Carlo
repetitions. Model based impulse responses are dashed blue and the shaded area represents
± one standard deviation confidence intervals for the estimated impulse responses. The VAR
based impulse responses are able to capture the model based dynamics following a news
shock. Output and its components, total hours as well as share prices, are all estimated
to respond positively while the VAR correctly identifies the negative response of net
trade. The VARs somewhat underestimate the magnitude of macroeconomic effects of a news
shock, particularly at longer horizons. This bias is probably related to the truncation of
the empirical model, as we only use two lags. When we expand the lag order to 4, this bias
almost disappears. Nevertheless, the theoretical impulse responses almost always lie
within the range of estimated impulse responses. These result suggest that our
identification successfully recovers news shocks. As in Barsky and Sims (2011), we argue
that our Monte Carlo results suggest that the invertibility or ‘fundamentalness' issue
raised by Fernndez-Villaverde et al. (2007) is not a major cause for concern for our work.

<h>EMPIRICAL RESULTS</h>
-----------------

In this section, we discuss impulse responses and forecast error variance decompositions
obtained from the structural VAR. Fig. 4 shows the estimated impulse responses in four
countries for TFP, output, consumption, total hours, investment, net trade and stock
prices. The grey shaded area represents 16th and 84th quantiles. As per our identification
restrictions, TFP remains constant for two periods and increases after the zero
restrictions end, and consumption and stock prices increase on impact. After the
identification restriction, the impact of the news shock is significantly positive for all
these three variables. The quantitative impact of the news shock is similar for TFP and
consumption in all countries. Possibly reflecting their volatility, the impact response of
stock prices are one order of magnitude higher than the response of TFP. Now consider the
response of other variables which are not subject to any identification restrictions. A
first robust finding is that in all countries, output is estimated to increase in response
to news. Except for New Zealand, output rises on impact. This is, for example, contrary to
Barsky and Sims (2011) who find that, in the US, the output response to a news about
future TFP tracks, but does not anticipate the movements in the estimated path of TFP. In
our sample of small open economies, positive news about future TFP creates an economic
boom on impact and its positive effects on output are estimated to be persistent. Second,
total hours and investment are also estimated to persistently increase after a news shock.
There is, however, somewhat more heterogeneity in the response of these two variables. In
the case of the United Kingdom, in particular, the response of these two variables seem to
be building up over time and less front loaded than in the other countries. The impulse
responses described so far imply that, for the small open economies we consider, news
shock generate a positive co-movement between output, consumption, investment and total
hours. Third, net trade is countercyclical in all countries except Australia following a
positive news shock, with some differences in the initial responses. Except for Canada,
the initial response of net trade is small and is followed with further deteriorations.
Comparing Figs. 1 and 4 shows that the estimated impulse responses are qualitatively
similar to those of our model. In both cases, there is co-movement between GDP,
consumption, investment and hours as well as a counter-cyclical trade balance. Model and
data do, however, differ with respect to the persistence of GDP, consumption and hours as
well as with respect to the magnitude of the response of share prices. Compared to the
data, the model predicts a more persistent response for GDP, consumption and hours and a
less volatile one for share prices. We now turn to the relative importance of the
identified news shocks in shaping the business cycle dynamics in our set of small open
economies. Table 1 reports the share of the news shock in the forecast error variance
decomposition for the seven variables in the VAR. The news shock accounts for between 6%
to 40% of the 10-quarter ahead forecast error variance of GDP. For consumption, the
figures are between 13% and 42%, and for investment between 11% and 44%. The shock also
accounts for between 7% and 20% of the 10-quarter ahead forecast error variance of net
trade. The large range of these results reflects heterogeneity between countries. In the
United Kingdom, the contribution of new shocks to the 10-quarter ahead forecast error
variance of GDP is much greater than in Australia, Canada or New Zealand. In New Zealand,
news shocks appear to play only a minor role. Whereas in the UK, they account for around
40% of the 10-quarter ahead forecast error variance of GDP, in New Zealand these shocks
only contribute around 6%. The role of news shocks in Australian and Canadian GDP is more
important than in New Zealand, but in both of these countries the forecast error variance
is still only about a two-thirds to half of that of the UK. That country-specific news
shocks are somewhat less important in the smaller and more open economies in our sample is
in line with the well documented importance of foreign shocks for these economies, see for
instance Justiniano and Preston (2010).

<hs>  News shocks and relative prices</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The choice of variables in our baseline VAR is determined by our theoretical model. As
such, we abstract from relative price movements and focus on net trade. In Fig. 5, we
examine a VAR augmented by two measures of relative prices, country i’s real exchange rate
vis-a-vis the United States and the terms of trade measured as the relative price of
exports to imports. In both measures, an increase denotes an appreciation. We also replace
net trade by real exports and real imports. In the VAR, the response of the real exchange
rate is not restricted, while the identification scheme is the same as our baseline
formulation. For all countries, the median response the real exchange rate to news shock
is an initial real appreciation. This appreciation is, however, relatively short lived and
not statistically significant for New Zealand. As the news about TFP is realised and TFP
increases, the real exchange rate depreciates as the increased supply of home produced
goods depresses its relative price. The qualitative dynamics of the other variables in our
VAR remain unchanged. For Canada and the UK, we also observe a significant appreciation of
the terms of trade. For our two antipodean commodity exporters, the initial response of
the terms of trade is not statistically significant. This suggests that for these small
open economies, the terms of trade is exogenous. For Canada and the UK, the real
appreciation of the terms of trade suggests that the observed real exchange rate
appreciation is not attributable to an increase in the relative price of non-traded goods.

<hs>  News shocks and behaviour of imports and exports</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

So far, our analysis suggests that, except for Australia, news shocks cause a worsening of
the net trade position. This is in line with our theoretical model. In a small open
economy, the demand for exported goods depends on its relative price and foreign aggregate
demand. In Fig. 5, we follow Corsetti et al. (2014) and analyse real exports and real
imports separately. For all countries in our sample, a positive news shock is associated
with an increase in both real imports and real exports. Except for Australia, the response
of imports is greater than the response of exports. Figs. 4 and 5 suggest that a
consistent picture emerges regarding macroeconomic dynamics conditional on news shocks in
small open economies. Our results indicate that positive news shocks about future TFP are
associated with initial increases in output, consumption, investment, total hours, stock
prices and are associated with countercyclical net trade dynamics. These results appear to
be in contrast with the recent empirical work focusing on the effect of TFP news shock on
the US economy.

<h>CONCLUSION</h>
----------

News about future TFP can be a source of business cycle fluctuations in small open
economies. For a set of advanced small open economies, we show that news about future TFP
causes positive co-movement between GDP, hours, consumption and investment. News shocks
are also associated with counter-cyclical current accounts. This is in contrast with
previous studies focusing on the US economy in which news about future productivity are
not associated with economic booms. We also find that the contribution of country specific
news shock in the forecast error variance decomposition of macroeconomic variables is
relatively modest. This is possibly due to larger share of foreign variables in driving
business cycle dynamics in these small open economies. In addition to our empirical
contribution, we also put forward a theoretical small open economy model that is able to
generate business cycles from news shocks to TFP. We introduce financial frictions, akin
to those in Jermann and Quadrini (2012) as a mechanism to generate the positive co-
movement between hours worked and consumption that is a challenge for canonical small open
economy models. Our modelling approach is deliberately parsimonious in order to put
forward a particular channel in generating news-driven business cycles.


<h>REFERENCES</h>
----------

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<ART>On the economics of electrical storage for variable renewable energy sources
============================================================================

Authors: Alexander Zerrahn, Wolf Peter Schill, Claudia Kemfert
DOI: 10.1016/j.euroecorev.2018.07.004
Year: 2018  |  Pages: 259-279
ASJC codes: 2002, 2003
Keywords: Energy storage, Solar, Variable renewable energy sources, Wind

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

The use of renewable energy sources is a major strategy to mitigate climate change. Yet Sinn (2017) argues that excessive electrical storage requirements limit the further expansion of variable wind and solar energy. We question, and alter, strong implicit assumptions of Sinn's approach and find that storage needs are considerably lower, up to two orders of magnitude. First, we move away from corner solutions by allowing for combinations of storage and renewable curtailment. Second, we specify a parsimonious optimization model that explicitly considers an economic efficiency perspective. We conclude that electrical storage is unlikely to limit the transition to renewable energy.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

In the 2015 Paris Agreement, the world agreed on ambitious targets for reducing greenhouse
gas emissions to combat climate change (United Nations, 2015). The use of renewable energy
sources is a major strategy for decarbonizing the global economy. As the potentials of
hydro, biomass or geothermal energy are limited in many countries, wind power and solar
photovoltaics (PV) play an increasing role. For example in Germany, often considered as a
frontrunner in the use of variable renewable energy sources, the government plans to
expand the share of renewable energy in gross electricity consumption to at least 80% by
2050, compared to 36% in 2017 and only around 3% in the early 1990s (Federal Ministry for
Economic Affairs and Energy, 2018). Closing this gap requires a massive further expansion
of wind and solar power. Opposed to dispatchable technologies like coal- or natural gas-
fired power plants that can produce whenever economically attractive, electricity
generation from wind and solar PV plants is variable: it depends on exogenous weather
conditions, the time of day, season, and location (Edenhofer et al., 2013; Joskow, 2011).
At the same time, maintaining power system stability requires to continuously ensure that
supply meets demand. The potential temporal mismatch of supply and demand raises two
fundamental questions: how to deal with variable renewable energy at times when there is
too much supply, and how to serve demand at times when supply is scarce (cf. also Brown et
al., 2018). Evidently, electrical storage can provide a solution, for instance, in the
form of batteries or pumped-hydro storage plants, allowing to shift energy over time. In a
recent analysis, Sinn (2017) argues that electrical storage requirements may become
excessive and could thus impede the further expansion of variable wind and solar power in
Germany. Based on historic time series of electricity demand and variable renewable energy
supply, he illustrates that without storage a fully renewable electricity supply would
imply not using 61% of the possible power generation from wind and solar generators. In
contrast, to avoid any “waste” of renewable energy, storage requirements to take up
renewable surplus energy1 quickly rise to vast numbers. Under such a strategy, current
German storage installations would not allow a share of wind and solar PV in electricity
demand greater than 30%.2 And for a fully renewable electricity supply, storage
requirements would be more than 400 times as high as the currently installed German
pumped-hydro storage capacity, and also much higher than the entire European potential to
build such plants (van de Vegte, 2015). These considerations deserve merit as they
illustrate essential properties of variable renewable energy sources, which gain relevance
throughout the world. Accordingly, economic research on renewables plays an important role
in informing policymakers, and Sinn’s analysis can be expected to be widely received both
in policy and academic circles.3 Yet the approach is based on strong implicit assumptions,
two of which are particularly questionable. First, it only considers two extreme cases in
which either all surplus energy is stored or none. In turn, either storage needs are
excessive or an excessive share of the available renewable energy is not used. An
economically efficient solution is likely to be located in between, i.e., combines some
amount of storage and some renewable curtailment. Second, it does not explicitly consider
an economic efficiency perspective. Sinn’s approach minimizes the storage energy capacity
under the constraint that renewables must satisfy a specified proportion of annual
electricity demand. Yet an economically efficient solution would seek to minimize the cost
to reach that specified proportion of renewables. Such a solution trades off the costs of
investments into storage plants, renewables that may get curtailed at times, and other
assets in the power market. We address, and alter, these implicit assumptions and show
that their effects are significant. Both results and conclusions change substantially.
When moving away from corner solutions, storage needs are up to two orders of magnitude
lower in a framework otherwise identical to Sinn (2017). Using a parsimonious optimization
model with a more suitable economic objective function that leads to first-best solutions,
we also find moderate storage requirements. They are even lower if we consider a future
broadening of the electricity sector, that is, an additional and flexible use of renewable
electricity in other sectors. Throughout the paper, we provide the economic intuition of
what drives storage requirements and use. Variable renewable energy sources are not only
variable in supply, they are also nearly free of variable cost. A wind or solar PV plant
generates electricity whenever the wind blows or the sun shines without requiring any
fuel. Curtailment of renewable energy denotes the operation of a wind or PV plant below
its actual temporary generation potential, that is, neither consuming the actually
available renewable energy in the moment of generation nor storing it for later use.
Analogously, also conventional power plants do not generate electricity at full capacity
at all times. The rationale is the following: if electricity demand is satisfied,
electrical storage can be used to take up renewable surplus energy. Yet integrating
increasing amounts of such surpluses requires disproportionately growing storage
capacities that are not valuable at most times (Denholm and Hand, 2011; Schill, 2014).
Thus, a corner solution avoiding any curtailment likely leads to inefficiently high
storage requirements. Instead, an efficient solution seeks to balance investments into
storage, renewables that get curtailed at times, and other capacities to minimize the
total cost of providing electricity. The remainder of this paper proceeds as follows: In
Section 2, we show that Sinn’s results are outliers compared to the established
literature. We then replicate his findings using open data and an open software tool in
Section 3. In Section 4, we extend the basic model to target solutions between the two
extreme cases. In Section 5, we devise a parsimonious model to endogenously determine
optimal storage and renewable capacities as well as renewable curtailment levels. In
Section 6, we discuss further relevant factors and flexibility options that influence
storage needs. Section 7 concludes that electrical storage requirements are not likely to
limit the transition to renewable energy.

<h>LITERATURE REVIEW</h>
-----------------

Researchers from various fields have addressed the nexus of variable renewable energy and
storage. Several review papers highlight different perspectives: the economic and
regulatory challenges of integrating variable renewable energy sources (Perez-Arriaga and
Batlle, 2012), features of techno-economic models required to generate policy-relevant
insights (Pfenninger et al., 2014),4 and the role of long-term storage (Blanco and Faaij,
2018). A synthesis of model-based analyses suggests that electrical storage requirements
for renewable energy integration are generally moderate. They may only increase
substantially in scenarios approaching a fully renewable energy system (Zerrahn and
Schill, 2017). For Germany, Sinn (2017) derives electrical storage capacity needs of 2,100
gigawatt hours (GWh) (5,800 GWh, 16,300 GWh), corresponding to 0.42% (1.15%, 3.23%) of
yearly electricity demand, to achieve combined shares of wind and solar power of 50% (68%,
89%). To put these numbers into perspective, we compare Sinn’s results with other studies
on future electricity systems with high shares of variable renewables. Also for Germany,
Schill and Zerrahn (2018) determine optimal storage requirements in long-run scenarios.
For 68% (78%, 88%) variable renewables,5 they arrive at 55 GWh (159 GWh, 436 GWh) storage,
corresponding to 0.01% (0.03%, 0.09%) of annual demand. Further results on storage needs
for the German energy transition are available among policy studies (Fraunhofer UMSICHT
and Fraunhofer IWES, 2014). A particularly influential study concludes that hardly any
additional storage investments are necessary in Germany and Europe in the short and medium
term (Pape et al., 2014): In 2050 scenarios with European shares of variable renewables
around 40% (45%, 55%), additional storage capacity between around 14 and 650 GWh is needed
(corresponding to 0.00% to 0.02% of annual demand), largely located outside Germany. A
long-term climate policy study commissioned by the German environmental ministry (BMUB)
also finds that around 170 GWh of pumped-hydro storage (0.02% to 0.03% of annual demand)
suffice to achieve variable renewable shares between 83% and 91% (Repenning et al., 2015).
For Europe, Scholz et al. (2017) derive cost-minimal storage capacities corresponding to
about 0.08% (0.28%) of yearly demand to achieve 74% (85%) variable renewables in a setting
with equal contributions of wind and solar power. Using the same numerical model, Cebulla
et al. (2017) derive larger storage needs of around 1% of yearly load at a variable
renewables share of 80% in a transmission-constrained European scenario. This number
decreases to 0.5% in case of increasing transmission capacity. In a recent long-term
scenario commissioned by the German energy ministry (BMWi), storage capacities in the size
of 0.01% of yearly demand are enough to achieve a pan-European renewable share of 65%
(Federal Ministry for Economic Affairs and Energy, 2017). For the U.S., MacDonald et al.
(2016) find that integrating up to 55% variable renewables in 2030 does not require any
electrical storage. Instead, pan-U.S. geographical balancing, facilitated by transmission
investments, mitigates the variability of wind and solar power. For the Pennsylvania-New
Jersey-Maryland market, Budischak et al. (2013) conclude that a large stock of electric
vehicle batteries, corresponding to 0.3% of yearly overall demand, would enable pushing
the renewables share to 99.9% in 99.9% of all hours. Using stationary batteries would—at
higher overall cost—require even less storage capacity. Jacobson et al. (2015) show that a
fully renewable (wind and solar power contributing 90%) U.S. energy system covering all
end use sectors would be possible with an electrical storage capacity smaller than 0.1% of
yearly electricity demand.6 For Texas, papers with different approaches also conclude on
moderate storage requirements: capacities corresponding to around 0.02% (0.06%, 0.14%) of
annual demand would suffice to integrate a combined share of wind and solar PV of 55%
(70%, 80%) with relatively low renewable curtailment (de Sisternes et al., 2016; Denholm
and Hand, 2011; Denholm and Mai, 2017). Safaei and Keith (2015) derive optimal storage
deployment of 0.10% of annual demand for a 66% wind power share. Based on our review, Fig.
1 plots the shares of variable renewable energy against storage energy requirements,
normalized by yearly energy demand, and contrasts them with Sinn’s findings.7 It also
includes the results of this paper from Section 5. Two findings stand out: first, storage
needs disproportionately grow with higher renewables shares. Therefore, the vertical axis
is provided in a logarithmic scale. This is driven by the distribution of surplus energy,
which has high peaks in only a few hours of the year and is very small or zero in most
other hours. Second, storage requirements found in the literature are considerably lower
than those calculated by Sinn (2017)—often by at least an order of magnitude. What drives
these large differences? One important factor is renewable curtailment; the data labels in
Fig. 1 provide the numbers in percent of the annually available renewable energy. Sinn
focuses on corner solutions without renewable curtailment as illustrated by the outer
line: the storage has to take up every potential kilowatt hour of surplus energy that
could be generated by wind power and solar PV generators, which leads to strongly
increasing storage requirements for growing shares of variable renewable energy sources.
By contrast, the literature agrees that a complete integration of variable renewable
energy is not desirable (see, in particular, Budischak et al., 2013; Schill, 2014; Schill
and Zerrahn, 2018; Ueckerdt et al., 2017). A combination of renewable capacity oversizing
and some temporary curtailment substitutes storage expansion when imposing economic
efficiency criteria, such as finding a technology portfolio for least-cost renewable
energy supply. In equilibrium, the marginal effects of adding another unit of storage and
adding another unit of renewable generation that gets curtailed at times are equal. A
social planner would thus trade off storage against renewable curtailment and other
options that can provide flexibility. Accordingly, renewable curtailment is not
necessarily inefficient. Beyond curtailment, further options on both the supply and demand
sides can provide flexibility for variable renewable energy sources and thus substitute
for electrical storage (Lund et al., 2015). These comprise geographical balancing (Fürsch
et al., 2013; Haller et al., 2012; MacDonald et al., 2016), demand-side management (Pape
et al., 2014; Schill and Zerrahn, 2018), and the flexible use of renewables in other
sectors such as heat or mobility (Budischak et al., 2013; Jacobson et al., 2015). To be
concise, we largely abstract from such options in our analysis, as in Sinn’s original
framework. We further discuss this avenue in Section 6. Our literature review highlights
two main insights: first, Sinn’s findings are outliers compared to the consensus of
established studies. Second, his extreme findings are driven by not considering relevant
economic trade-offs concerning the provision of flexibility, in particular by neglecting
potential renewable curtailment.

<h>REPLICATION AND INTUITION</h>
-------------------------

We first replicate the central results of Sinn’s analysis, using a spreadsheet tool and
open-source input data. Following recent discussions on good practice in the field of
energy research (Pfenninger, 2017; Pfenninger et al., 2018), we provide our tools and all
input parameters under a permissive open-source license in a public repository.8

<hs>  Focus of our analysis</hs>
  ~~~~~~~~~~~~~~~~~~~~~

In our replication, we focus on the central Section 6 in Sinn (2017). Here, he derives
storage requirements to integrate increasing shares of variable renewable energy from wind
and solar PV in final electricity demand, ranging between 16.6% and 89%. In Sections 7 and
8, he provides stylized geographical extensions of this approach; while these are
illustrative, we stick to the central model and its mechanics from Section 6.9 In Sections
2–4, Sinn suggests transforming variable renewable supply to a perfectly constant output
over all hours of a year. Such smoothing results in excessive storage needs. However,
there is no economic or technical reason for this kind of smoothing. It seems to be
inspired by the notion that renewable generators should mimic the characteristics of
conventional power plants. In this case, additional backup capacities (referred to as
“double structures”) would be obsolete. However, it is not clear why using existing backup
power plants should be less desirable than installing additional electrical storage; the
approach is silent about any efficiency or optimality criteria. The lack of practical
relevance is illustrated by the fact that resulting storage requirements cannot be
empirically observed in countries with high variable renewables shares like Denmark,
Ireland or Spain.10

<hs>  Replication using open data and an open software tool</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We derive input data from the Open Power System Data platform, which collects and provides
European electricity market data from official sources (Open Power System Data, 2017).
Input parameters comprise hourly time series of realized German electricity demand and
availability of onshore wind power and solar PV, defined as capacity factors between zero
and one. Electricity demand enters the analysis as inelastic, that is, we do not fit any
demand curves. This assumption follows Sinn (2017) and is also standard in much of the
literature.11 We calculate capacity factors by relating historic hourly feed-in to
installed renewable generation capacity in respective hours. As in Sinn (2017), all input
data is taken from the base year 2014. The approach aims at finding the smallest possible
storage size to integrate all renewable generation. It is equivalent to Sinn’s objective
of scaling the storage such that it is empty in at least one hour. The hourly storage use
pattern is shifted up and down until the minimum storage size is found. To avoid free
lunch, we require the storage level in the first and last hour of the year to be equal.
Using open data and open software tool, we are able to replicate Sinn’s central
findings.13 Additionally, we provide results for further shares of variable renewable
electricity ranging between 20 and 90%. Fig. 2 shows storage requirements for varying
shares of renewable electricity in final demand. Results from our calculations are given
in black, Sinn’s results in gray. Storage needs rise sharply if more renewable electricity
must be integrated. While current German pumped-hydro storage installations of somewhat
below 0.04 terawatt hours (TWh) would suffice to fully integrate almost 30% renewable
electricity, even moderate further increases in renewables would substantially drive up
storage requirements. For 50% variable renewables, they already amount to 2.1 TWh, that
is, they are two orders of magnitude higher. As Sinn does not provide his data and
calculations open-source, we cannot trace back the small numerical differences to our
findings to a specific reason; presumably, they arise due to slight differences in the
input data.

<hs>  (Non-)robustness</hs>
  ~~~~~~~~~~~~~~~~

We address the robustness of findings in a sensitivity analysis using different base
years. Both the time series of demand and the availability of renewable energy may change
substantially between years. To this end, we repeat the basic analysis using hourly time
series of demand and the renewables capacity factor from the base years 2012, 2013, 2015,
and 2016. Fig. 3 depicts the results: storage requirements turn out to be highly sensitive
to the choice of the base year. Taking data from 2014 yields the highest storage needs up
to a variable renewables share of 65%. In contrast, data from 2015 leads to the smallest
storage sizes up to 65% renewables. For instance, comparing the 50% renewables case,
storage installations are less than a fifth for 2015 data as compared to 2014 data. For a
high renewable penetration beyond 65%, data from the base year 2013 leads to the smallest
storage. Using 2014 data generally yields comparatively large storage capacities. We
explain the drivers of storage requirements below.

<hs>  Intuition: the residual load duration curve</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

To gain intuition what drives storage requirements, we use the concept of residual load
duration curves (RLDCs). Residual load—also referred to as net load—is defined as hourly
demand minus renewable feed-in in the respective hour. It is the remaining load that
conventional plants or storage installations must serve.14 A residual load duration curve
is a graphical representation of residual load of all 8760 hours of a year, sorted in
descending order. The positive integral of the curve corresponds to the energy that must
be provided by non-renewable energy, storage generation or imports. The RLDC concept is
prominent in the energy economics literature (compare also Ueckerdt et al., 2017). Fig. 4
shows RLDCs for the above analysis in case of 80% renewables, using 2014 as the base
year.15 The solid line shows residual load before storage use. To the right, below the
horizontal axis, residual load is negative, indicated by area A. In these hours, there is
a surplus of renewable generation. To the left, there are hours with positive residual
load, areas B and C. In these hours, there is relatively high demand and low renewable
energy generation. The dotted line shows the RLDC after storage use.16 The storage takes
up energy in hours of excess renewable supply and releases it in hours with excess demand.
Graphically, it shifts the surplus energy represented by area A to area B, which equals
the size of area A reduced by the storage’s efficiency losses. Area C represents the
annual residual load that must be served by other generators, for instance conventional or
dispatchable renewable plants. By assumption, it corresponds to 20% of total demand in
this case.17 Importantly, nothing forces the storage to shift energy to hours with highest
residual loads, that is, greatest scarcity, at the very left-hand side of the RLDC; the
operational heuristic prescribes to empty the storage as soon as residual demand is
positive again. With the present patterns of demand and renewable feed-in, it is unlikely
that an hour with very high residual load follows closely to an hour with renewable
surplus generation. The RLDC representation dissolves the temporal sequence of hours
during the year.

<h>STORAGE REQUIREMENTS UNDER RENEWABLE CURTAILMENT</h>
------------------------------------------------

The residual load duration curve illustrates the two challenges of integrating high shares
of variable renewable electricity: (i) on the left-hand side of the curve, there are hours
with high demand that variable renewables cannot directly supply; (ii) on the right-hand
side, there are hours with renewable surplus generation. Both sides of the RLDC have an
impact on storage requirements.

<hs>  Power-oriented renewable curtailment</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The RLDCs suggest that curtailment of renewable surpluses may reduce storage requirements.
We first devise a strategy that allows curtailment of all renewable energy surpluses
beyond a defined threshold. This threshold can be interpreted as the power capacity of a
storage (in megawatt, MW); this is the energy the storage can take up per hour—as opposed
to the energy capacity the storage can accommodate in total (in megawatt hours, MWh). This
distinction is an essential characteristic of any electric storage technology and missing
in Sinn (2017). In case of pumped-hydro storage, the power capacity describes the power of
the pumps or of the turbine to generate electricity; the energy capacity indicates the
volume (in energy terms) of the storage basin. We extend the basic model by a renewable
curtailment threshold, equivalent to the power capacity of the storage. If hourly surplus
generation is below the threshold, it is channeled into the storage; all renewable surplus
energy beyond the threshold is curtailed. Otherwise, the model is identical to Section 3
and storage use remains myopic. To gain some intuition, Fig. 5 shows RLDCs for 80%
renewables in final demand and a curtailment threshold of 44.1 gigawatt (GW), which leads
to curtailment of 5% of maximum yearly renewable generation. The threshold is indicated by
the horizontal solid gray part of the RLDC after renewable curtailment on the right-hand
side. Area D represents all renewable surplus that is curtailed. The storage shifts the
remaining surplus energy from area A to area B. The remaining energy demand, area C, is
supplied by other, unspecified technologies. This renewable curtailment strategy avoids
storing the most excessive surplus events. We iterate through combinations of minimum
renewable requirements and maximum allowed renewable curtailment. In doing so, the
spreadsheet model endogenously determines the curtailment threshold—or storage power
capacity—such that no more renewable energy is curtailed than maximally allowed. Fig. 6
shows the results. It is evident that increasing levels of renewable curtailment lead to
lower storage requirements. The decrease is close to linear though somewhat convex. For
instance, while a complete integration of 50% variable renewable electricity triggers 2.1
TWh storage energy capacity, allowing curtailment of 5% of the annual renewable generation
reduces storage needs to 0.3 TWh. Specifically, we provide solutions that lie between the
two extremes “no renewable curtailment” and “no storage”, which Sinn (2017) only
considers. The vertical axis of Fig. 6 indicates storage requirements for the corner
solution if no renewable curtailment is allowed. The numbers are identical to those that
we replicate from Sinn’s approach (compare Fig. 2 and the right panel of his Table 1). The
horizontal axis shows renewable curtailment levels for the corner solution if no storage
is allowed. Here, we also replicate Sinn’s findings on “efficiency losses” that are given
in the left panel of his Table 1. For instance, for 50% renewables, our model returns a
renewable curtailment between 6.0 and 6.5%, as indicated by the point where the solid gray
line intersects the horizontal axis in Fig. 6. For the same case, Sinn determines an
“efficiency” of 93.8%, which corresponds to curtailment of 6.2%.18 Thus, we provide a
solution space combining curtailment and storage that lies between the two extreme cases.
For other base years, results are qualitatively unchanged; however, they exhibit great
variation concerning the level of required storage. To achieve the same share of renewable
energy in final demand, the required renewable capacities are necessarily higher when
allowing for curtailment, that is, if some of the available energy is not used. However,
this increase is moderate, as Fig. 7 shows. For instance, achieving 50% renewable energy
in final demand requires 214 GW renewables without curtailment. With 5% curtailment, the
necessary renewable capacities are somewhat higher, at 226 GW. Yet renewable curtailment
does not increase the necessary backup capacities to supply the remaining residual
electricity demand after storage. They are no larger than in the case without renewable
curtailment. Inspecting the left-most part of the RLDCs in Figs. 4 and 5, there is also no
reason to assume so.19

<hs>  Energy-oriented renewable curtailment</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

While the power-oriented storage strategy—curtailing renewable surplus whenever it exceeds
a defined threshold—seems plausible, it may not be optimal with respect to finding the
smallest required storage energy capacity. Given historic input data, it turns out that
extended periods of renewable surpluses in contiguous hours determine the maximum energy
capacity of the storage, and not single periods with the highest surplus generation. For
instance, storing a moderate surplus in ten consecutive hours may require more storage
than storing an extreme surplus event in one hour. Therefore, we alternatively implement
an energy-oriented renewable curtailment strategy. The storage operational pattern remains
myopic and is identical to the above cases; however, renewable curtailment occurs if and
only if the storage is fully loaded. Thus, it targets a minimum energy capacity
requirement. Again, we iterate through minimum renewable requirements and maximum
renewable curtailment constraints to explore the solution space and endogenously determine
minimum storage capacities. To provide some intuition, Fig. 8 shows the resulting residual
load duration curves for the case of 80% renewables and a maximum curtailment of 5% of the
annual renewable energy. Curtailed energy, area D, is identical to the one under the
power-oriented renewable curtailment strategy, area D in Fig. 6. However, renewable
curtailment is concentrated in hours in which surpluses trigger the highest storage
requirements; these are not necessarily the hours with the highest surplus generation.
Storage shifts the remaining surplus generation, area A, to hours with positive residual
load, area B. Note that renewable curtailment and the storage operational pattern are
still myopic and deterministic, that is, they do not require perfect foresight: surplus
energy is charged into the storage as long as there are free capacities, and is curtailed
otherwise. The stored energy serves residual load as soon as it is positive again. Fig. 9
shows the resulting storage requirements for varying minimum shares of renewable energy.
Overall, storage requirements decrease substantially even if only small levels of
renewable curtailment are allowed. Again, the intersection points with the axes represent
Sinn’s corner solutions: on the vertical axis all renewable energy must be integrated; on
the horizontal axis no storage is available. Any combination of both options yields
significantly lower storage needs; the decrease is much more convex than under the power-
oriented renewable curtailment strategy; already a small curtailment budget triggers a
large effect.20 For instance, while a complete integration of 50% variable renewable
electricity requires 2.1 TWh storage energy capacity, allowing for 5% renewable
curtailment reduces storage needs to 0.019 TWh, or 19 GWh. This is one order of magnitude
lower than under the power-oriented curtailment strategy, two orders of magnitude lower
than without renewable curtailment, and less than the pumped-hydro power capacity
installed in Germany by 2018. Allowing 11% curtailment, 41 GWh of storage, slightly more
than installed in Germany by 2018, would suffice to reach 60% variable renewable energy.

<h>COST-MINIMAL STORAGE REQUIREMENTS</h>
---------------------------------

The data-driven analysis in Section 4 alters one important implicit assumption of Sinn’s
approach: plausible solutions lie between the two corner solutions of no renewable
curtailment or no storage. However, the approach is still unlikely to result in an
efficient market outcome because of the objective function used. From an economic
perspective, finding least-cost solutions is relevant, that is, cost-minimal combinations
of conventional and renewable generation, renewable curtailment, and electrical storage.21
As we also include a stylized representation of conventional generators, we explicitly
address what Sinn refers to as “double structure buffering.” In this context, both storage
energy capacity (in MWh) and storage power capacity (in MW) matter with respect to
costs.22 To find optimal solutions, we employ a stylized and parsimonious numerical
optimization model.23 We provide the source code and all input data under a permissive
open-source license in a public repository.24 The economic optimization approach addresses
both challenges of renewable energy integration. First, it delivers an efficient solution
to the trade-off how much and when renewable surplus energy to curtail, and how much and
when to store. This corresponds to the right-hand side of the residual load duration
curve. Second, it determines efficient conventional, renewable, and storage capacities to
serve demand at any point in time; this corresponds to the left-hand side of the residual
load duration curve. The results of the cost minimization model can be interpreted as
long-run equilibria under the assumption of perfect competition and complete information.
The model thus mimics a first-best social planner approach.

<hs>  The model</hs>
  ~~~~~~~~~

The numerical model minimizes the total costs of satisfying electricity demand in every
hour h of a year. The objective function (1) sums the products of specific investment
costs κi and capacity entry N of storage, differentiated by energy Nse and power Nsp,
renewables Nr, and conventional capacity Nc. Throughout the model, upper-case Roman
letters indicate variables. For conciseness, we consider one stylized technology for
variable renewables that aggregates the generation patterns of onshore wind power and
solar PV,25 and two stylized conventional technologies c ∈ {base, peak}, parameterized to
lignite and natural gas plants. Base generators incur high capacity costs and low variable
costs, and vice versa for peak plants. We parameterize storage according to pumped-hydro
storage, which features relatively high costs for power capacity κi,sp and relatively low
costs for energy capacity κi,se. By focusing on pumped-hydro storage, we follow the
narrative in Sinn (2017). Moreover, it is a mature technology and its cost structure
renders it a favorable medium-term storage. This complements the variability of renewables
well, especially with regard to the diurnal fluctuations of PV.26 Investment costs are
annualized using typical lifetimes of power plants. For simplicity, we abstract from the
lumpiness of investments. All variables are continuous and positive. Renewable energy does
not incur any variable costs. We also do not impose any costs for curtailment of
renewables. As the objective function comprises the investment costs of renewable plants,
it accounts for the full cost of renewable energy irrespective whether it eventually
satisfies demand or is curtailed at times.27 By analogy, also the use of conventional
plants below capacity does not receive any penalty in the objective function. The model is
a linear program and solved numerically to global optimality. The result is a cost-minimal
combination of renewable, conventional, and storage capacity investments as well as their
optimal hourly dispatch. Specifically, two strategies can increase the required minimum
share of renewables: the use of storage to integrate surpluses, or larger renewable
capacities plus curtailment. The model solves this trade-off endogenously. Note that,
opposed to the myopic models in Section 4, this approach requires the assumption of
perfect foresight to optimally schedule the release of energy from the storage.29

<hs>  Intuition</hs>
  ~~~~~~~~~

To again provide some intuition before discussing numerical results, Fig. 10 plots the
resulting RLDCs for the 80% renewables case. If capacity entry is costly with respect to
both storage power and storage energy, the optimal solution combines both channels
analyzed in Section 4. Areas D1 and D2 represent the curtailed renewable energy. The kink
to the right is driven by power-oriented curtailment, compare Fig. 5. The renewable
surplus gets curtailed beyond the threshold of 46 GW, as the shaded area D1 indicates,
limited by the optimal storage power capacity. Curtailment of renewable surplus D2 is
driven by energy-oriented renewable curtailment, compare Fig. 8, targeted at limiting the
storage energy capacity. Area A represents the stored renewable surplus energy, which the
storage shifts to hours with positive residual load. The optimal release of the stored
renewable energy surpluses economically balances three uses: First, the energy shifted to
area B1 reduces generation—and according variable costs—of the base technology, which
otherwise operates whenever residual load is positive. Second, the energy shifted to area
B2 reduces variable costs of the peak technology. Base capacity is 29.4 GW, indicated by
the horizontal part of the dotted line; beyond, the peak plant with higher variable costs
additionally generates electricity. Third, the energy shifted to area B3 replaces capacity
entry—and respective cost—of the peak technology. If there was no storage, additional
generation capacity would have to satisfy the demand exceeding 53.5 GW, indicated by the
left-most horizontal part of the dotted line.30 Thus, the cost-minimization model
illustrates two economic values of electrical storage beyond avoiding renewable
curtailment in a concise way. First, an arbitrage value materializes when stored renewable
surplus energy replaces variable costs of other generators, in particular fuel costs.
Second, a capacity value materializes when stored renewable surplus energy replaces
conventional power plant capacities that otherwise would have to be provided for hours of
residual load peaks. Still, only renewable energy can enter the storage by assumption.
Opening up the storage for conventional energy would strengthen both economic values. In
reality, no reason prohibits such operation.31

<hs>  Results</hs>
  ~~~~~~~

Fig. 11 summarizes the results of the parsimonious optimization model. Optimal storage
capacities, both with respect to energy and power, rise with the share of variable
renewable energy. However, overall storage requirements remain moderate. For instance, a
storage energy capacity of 35 GWh suffices to achieve a share of 50% renewables in final
demand. This is about two orders of magnitude less than in Sinn’s analysis, but slightly
more than when targeting minimum storage requirements because the model considers
additional values of storage. Yet it is still less than installed in Germany by 2018.
Analogous findings prevail for other renewables shares.32 When increasing the targeted
renewables share, the optimal storage energy capacity grows much faster than the optimal
storage power capacity. For 50% renewables, 35 GWh energy are accompanied by about 6 GW
storage power. Dividing energy by power yields an energy-to-power (E/P) ratio of about 6
hours. The E/P ratio is an important metric to characterize a storage technology and
reflects its temporal layout: a 6 hours storage is a typical short-to-medium-term storage
to compensate diurnal fluctuations, such as of solar PV generation. If it is completely
charged, it can generate electricity for 6 hours at maximum power rating.33 For higher
renewables shares, the E/P ratio increases to reach about 19 hours for 90% renewables.
This highlights the importance of considering both rather inexpensive storage energy and
rather expensive storage power separately. Moreover, no need for a true long-term storage
arises, that is, storing energy for weeks or months. Optimal endogenous renewable
curtailment also grows with higher minimum renewables shares. As such, the economics of
renewable electricity provide no reason why curtailment should be avoided. It can be more
efficient not to use available renewable energy at times despite costly investment into
wind and PV plants. The optimal solution combines conventional plants, storage, and
renewables, part of which being curtailed at times.

<hs>  Extension: flexible sector coupling (power-to-x)</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In future low-carbon energy systems, renewable electricity supply considered as surplus
energy in the above framework is likely to be highly valuable for new uses. Merging
electricity, heating, and transport sectors can not only provide flexibility for
integrating variable renewables into the power market, but can also contribute to
decarbonizing these other sectors (Mathiesen et al., 2015). This concept, often referred
to as sector coupling, comprises using renewable electricity, for example, for residential
heating (see Bloess et al., 2018, for an overview of the recent literature) or for
electric mobility (Richardson, 2013). Moreover, renewable electricity can also be used to
produce other energy carriers, such as hydrogen or synthetic gaseous or liquid fuels, by
means of electrolysis (Schiebahn et al., 2015). Such sector coupling options are often
referred to as power-to-x (or P2X). They can lower electrical storage requirements if the
new loads are sufficiently flexible and the additional demand can be shifted to periods in
which renewable availability is high. Fig. 12 summarizes the results. For most renewables
shares, both optimal storage capacities and renewable curtailment rates are substantially
lower in case power-to-x technologies are included. For instance, for 50% renewables, the
storage energy capacity drops from 35 GWh to 4 GWh and renewable curtailment from 5% to
below 1%. Electrical storage requirements are lower up to a renewables share of 85%. In
the 90% renewable case, storage needs are the same as in the case without power-to-x, as
the additional demand can be completely satisfied from renewable surplus generation that
would otherwise be curtailed. The rationale is the following: in the 50% renewables case,
wind and solar capacities rise from 223 GW to 298 GW to supply part of the additional
power-to-x demand. Another part of the additional demand is satisfied by renewable
electricity previously curtailed or stored. Accordingly, both storage needs and renewable
curtailment rates are substantially lower in most cases.35 As we assume power-to-x to be
perfectly flexible, the diminishing effects on storage requirements and renewable
curtailment constitute an upper bound for less flexible real-world applications. However,
they illustrate that flexible sector coupling could substantially drive down electrical
storage needs. If additional flexible electricity demand emerges that contributes to
decarbonizing other energy sectors, then renewable surplus generation becomes a valuable
resource.36

<h>DISCUSSION</h>
----------

Departing from Sinn (2017), we implement small but relevant changes to move his the setup
away from corner solutions. The impact is substantial and reduces storage needs up to two
orders of magnitude. At the same time, our analysis remains stylized and tractable. In the
following, we highlight further important points that researchers should consider when
analyzing storage needs to integrate variable renewable electricity, both against the
background of Sinn’s analysis and the large body of academic literature (Brown et al.,
2018). First, the definition of efficiency should be clarified when it comes to variable
renewable energy sources. Sinn (2017) seems to refer to inefficiency as both curtailment
of renewables and storage use as such; the first motivated by avoiding waste, the second
by avoiding backup capacities (referred to as “double structure buffering”).37 However, a
welfare economic approach should rather target the least-cost provision of electricity for
given minimum renewable energy constraints. The result is a combination of conventional
and renewable plants, storage, and curtailment of a certain amount of renewable energy.
Why the one or the other should be “inefficient” is unclear. In the optimum, the marginal
cost of further expanding storage, renewables that are curtailed at times, and
conventional capacities is equal. Which shares of renewable energy are optimal when also
considering external costs, for instance, arising from climate change, local emissions or
land use change, whether the market achieves this solution, or which regulatory measures
are required is another issue left for analysis and discussion elsewhere. Second,
electrical storage has values beyond arbitrage. It can provide firm capacity and thus
reduce the need for backup plants (see Section 5.2), provide balancing reserves and other
ancillary services to maintain power system stability, and may also help mitigating grid
constraints. Third, other types of energy storage are relevant beyond pumped-hydro. These
comprise batteries, which could become much cheaper in the future (Schmidt et al.,
2017),38 or power-to-gas storage. Specifically, different storage technologies have
different costs for power and energy capacities. While batteries are relatively cheap in
power, they are expensive in energy, and vice versa for power-to-gas. Thus, electrical
storage technologies have different optimal E/P ratios: batteries are generally suited for
short-term storage of a few hours, pumped hydro for around six to ten hours, and power-to-
gas for longer periods. An optimal deployment of different storage types can address
different types of renewable fluctuations, for example, intra-hourly, diurnal or even
seasonal (Safaei and Keith, 2015; Scholz et al., 2017; Zerrahn and Schill, 2017). Such a
differentiated storage fleet also tends to be smaller and cheaper. Fourth, scaling up
historical feed-in time series of a fixed proportion of wind and solar power tends to
over-estimate flexibility requirements. Both market forces and the renewables support
scheme in Germany tend to incentivize renewable generation when prices are higher and
supply is, accordingly, scarce. Such system-friendly renewables comprise wind turbines
that dis-proportionally produce electricity when wind speeds are low, both due to their
location and technical layout (May, 2017). A similar argument holds for solar PV panels,
which may be directed such that they generate more electricity in morning or afternoon
hours. Even more relevant, offshore wind turbines have much smoother generation patterns
and higher full-load hours than onshore wind parks.39 The sensitivity toward the base year
in Section 3 further illustrates the relevance of appropriate input data choices. Ideally,
analyses should be based on bottom-up weather data covering as many years as possible
(Staffell and Pfenninger, 2016). Fifth, further electricity market integration across
national borders generally yields smoother residual load. When balanced over greater
geographical areas, the variability of wind, solar, and demand tends to be evened out
(Cebulla et al., 2017; Fürsch et al., 2013; Haller et al., 2012; MacDonald et al., 2016).
This results in smoother residual load patterns and lower storage requirements. Finally, a
temporally more flexible demand can also substitute electrical storage (Denholm and Hand,
2011; Pape et al., 2014; Schill and Zerrahn, 2018). If a more variable electricity supply
triggers more volatile prices, and these prices are passed through to consumers, then the
demand side should have increasing incentives to consume more flexibly and profit from
arbitrage gains.

<h>CONCLUSIONS</h>
-----------

The use of renewable energy is a major strategy to mitigate greenhouse gas emissions,
reduce fossil fuel imports, and create a sustainable energy system. However, integrating
growing shares of variable wind and solar power in electricity markets poses increasing
challenges. Electrical storage is an important—albeit not the only—option to address the
mismatching time profiles of variable renewable supply and electric demand. In a recent
analysis, Sinn (2017) calculates storage needs in a German setting and finds vastly
growing electrical storage requirements, already for renewable supply shares only
moderately greater than currently the case in Germany. Based on these findings, he
suggests that electrical storage may limit the further expansion of variable renewable
energy sources. While Sinn’s illustrations deserve merit, the findings are not backed up
by the literature. A large body of techno-economic studies conclude on substantially lower
storage needs, also for high shares of variable renewables. An important reason for Sinn’s
deviating findings is that he only considers corner solutions—either no storage, resulting
in vast renewable curtailment, or no curtailment, resulting in excessive storage
requirements. We show that addressing these implicit assumptions matters: both results and
conclusions change substantially. Our analysis, based on open-source tools and open data,
concludes that storage needs are lower by up to two orders of magnitude. Our findings are
in line with most of the literature. Cost-efficient solutions optimally combine renewable
capacity expansion, renewable curtailment, and electrical storage. We also illustrate that
electrical storage needs may decrease further if the electricity sector is broadened to
also include flexible additional demand, for example related to heating, mobility or
hydrogen production. While we demonstrate that such power-to-x options may substantially
change the picture, further and more detailed research on this avenue would be desirable.
All things considered, we conclude that electrical storage requirements do not limit the
further expansion of variable renewable energy sources.


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<ART>On the social inappropriateness of discrimination
=================================================

Authors: Abigail Barr, Tom Lane, Daniele Nosenzo
DOI: 10.1016/j.jpubeco.2018.06.004
Year: 2018  |  Pages: 153-164
ASJC codes: 2002, 2003
Keywords: Allocator game, Discrimination, Krupka-Weber method, Social norms

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We experimentally investigate the relationship between discriminatory behaviour and the perceived social inappropriateness of discrimination. We conjecture that discrimination will be weaker when social norms oppose it. Our results support this prediction. Using a Krupka-Weber social norm elicitation task, we find participants perceive it to be more socially inappropriate to discriminate on the basis of nationality than on the basis of social identities artificially induced using a trivial minimal group technique. Correspondingly, we find that participants discriminate more in the artificial identity setting. Our results suggest norms and the preference to comply with them affect discriminatory decisions and that the social inappropriateness of discrimination moderates discriminatory behaviour.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Economic theories seeking to explain discrimination focus on two mechanisms. First, in the
presence of incomplete information, profit- or income-maximizing agents use aggregate
group characteristics to form statistical beliefs about individual characteristics and
then act in accordance with those beliefs by, potentially, treating members of different
groups differentially (Arrow, 1972). Second, individuals are assumed to derive direct
utility from favouring certain groups relative to others, i.e. they are assumed to have a
‘taste for discrimination’ (Becker, 1957). Such tastes explain why discrimination is
observed even in settings where asymmetric or incomplete information is not an issue (e.g.
Chen and Li, 2009; Abbink and Harris, 2012). The focus of our paper is on this second form
of discrimination, taste-based discrimination, and in particular on the psychological
foundations of the tastes or preferences for discrimination, which have received
remarkably little attention in the literature. Specifically, in this paper we use
experimental methods to investigate whether tastes for discrimination are systematically
associated with social norms, i.e. collectively recognised rules of behaviour that define
which actions are viewed as socially appropriate within a specific social group.1 As we
discuss further below, there may be a host of factors that shape the tastes for
discrimination, including direct altruism towards members of one's own social group. The
key contribution of our paper is to provide evidence that one important taste-shaping
factor is a norm-based mechanism that regulates the extent to which actions that favour
one's own group relative to others are regarded as permissible and appropriate. Uncovering
this normative component is an important step towards understanding how patterns of taste-
based discrimination are shaped. If social norms moderate the taste for discrimination,
the incidence of discriminatory behaviour should positively correlate with beliefs about
the appropriateness of discrimination. Similar correlations have been found in relation to
other types of economic behaviour. Following Krupka and Weber (2013), lab and lab-in-the-
field experiments have shown that in a variety of economic contexts people are more likely
to take an action the more socially appropriate they perceive it to be (e.g. Burks and
Krupka, 2012 – corporate ethics; Gächter et al., 2013 – gift-exchange; Krupka et al., 2016
– informal contract enforcement; Banerjee, 2016 – bribery). There is also evidence from
econometric research (e.g. Buonanno et al., 2009) and natural field experiments (e.g.
Allcott, 2011) suggesting norms drive behaviour outside the lab. Thus, in driving
behaviour, social norms may effectively substitute for laws (e.g. Huang and Wu, 1994), or
may complement them (e.g. Sunstein, 1990; Kübler, 2001; Lazzarini et al., 2004; Posner,
2009; Benabou and Tirole, 2011). However, a correlation between individuals' beliefs about
the appropriateness of discrimination and the prevalence of discriminatory behaviour is a
challenge to document empirically using naturally occurring data, not least of all because
of the difficulties associated with accurately measuring such beliefs.2 Occasionally,
attitudinal surveys include questions that can be interpreted as eliciting respondents'
perceptions of the appropriateness of discrimination. For instance, the 2002 wave of the
Scottish Social Attitudes Survey asked respondents whether they believed that ‘sometimes
there is good reason for people to be prejudiced against certain groups’. One can
interpret responses to this question as a proxy for the perceived social appropriateness
of discrimination. Using this interpretation, we calculated the percentage of residents in
each local authority area of Scotland who agreed with the statement. For each area, Fig. 1
plots this variable against the number of racist incidents,3 per 100 non-white residents,4
reported to the police in the financial year 2003–4 (Scottish Executive Statistical
Bulletin, 2007). A correlation coefficient of 0.27 between the two variables suggests a
positive relationship between the social appropriateness of racial discrimination and the
incidence of racially discriminatory behaviour, which is consistent with the notion that
norms moderate the taste of discrimination. The acceptability of prejudice-based humour
has sometimes been used as a proxy for the normative appropriateness of discrimination
(see, e.g., Crandall et al., 2002). Fig. 2 plots, over the period 2004 to 2014, the
frequency of Google searches in the US for ‘N***** jokes’ (we apply the censorship for
this paper; the original search term was uncensored5), as a proportion of all Google
searches in the US (Google Trends, 2016). Searching for racist jokes about black people
can be treated as evidence that the searcher perceives discrimination against black people
to be socially appropriate. Fig. 2 also plots, on an annual basis over the same period,
the number of incidents in the US involving hate crimes motivated by an anti-black bias
that were reported to the FBI, per every 100 people living in areas where the hate crimes
are reported (United States Department of Justice, 2015).6 Both the frequency of anti-
black joke searches and the rate of anti-black hate crime incidents declined considerably
over the period. This is suggestive of a positive relationship in the US between the
change over time in the social appropriateness of discrimination against black people and
the change over time in discriminatory behaviour against black people. In spite of these
examples, the paucity of useful naturally occurring data with which to investigate the
empirical relevance of norms for discriminatory behaviour advances the case for using
experimental methods to address the question. Our paper does this, with an empirical
strategy relying on four main elements. First, we use standard experimental techniques to
prime participants to think about particular dimensions of their identities. The priming
aims to trigger a process of social identification by encouraging subjects to identify
with half of the participants in their experimental session and not with the other half.
Second, in the decision-making phase of the experiment we ask subjects to distribute a
given amount of money between two potential recipients, one an individual sharing their
primed identity (‘in-group’), the other an individual not sharing their primed identity
(‘out-group’). This simple allocation task allows us to measure discrimination as the
extent to which individuals are willing to favour members of their own social group at the
expense of the out-group. Third, crucially, we exogenously vary the dimension of identity
that is primed. We do this across two treatments that we designed to vary the perceived
appropriateness of discriminating in favour of the in-group and against the out-group,
while holding other aspects of the decision-making context constant.7 Under one treatment,
social identities are based on nationality; we form groups in the laboratory based on
whether participants are British or Chinese. Under the other treatment, social identities
are entirely artificial; groups are formed according to the colour of ball that each
participant draws blindly from a bag. We expect the norms that mandate how a decision-
maker should treat in-groups and out-groups in our experiment to differ across the two
treatments. Specifically, we expect discrimination against out-group and in favour of in-
group members to be perceived as less appropriate when identity groups are formed on the
basis of nationality than when they are artificially formed on the basis of the colour of
balls randomly picked. Indeed, when identity groups are artificially formed, participants
have no directly relevant social norm to which to refer for guidance about the social
appropriateness of discrimination. If this is the case, our exogenous manipulation varies
the strength of the norm relating to discrimination across our treatments and, if
discrimination is systematically shaped by norms, we thus expect discrimination to be
stronger between the artificial groups. Fourth, as well as measuring discrimination, we
directly measure the perceived social appropriateness of discrimination in each treatment.
We do this by employing the ‘norm-elicitation’ task introduced by Krupka and Weber (2013),
in which participants are described the allocator game and are asked to evaluate the
social appropriateness of each and every possible action available to the allocator. We
use this norm-elicitation task to construct an incentivized measure of the extent to which
participants' perceptions of the appropriateness of discrimination vary across our two
treatments and to examine the extent to which these differences in perceived
appropriateness translate into differences in discriminatory behaviour in the allocation
task. Our results show that, in both treatments, discriminatory actions are viewed as
socially inappropriate. However, as expected, discrimination is perceived to be
significantly less appropriate in the nationality treatment compared to the artificial
identity treatment. The results of the decision task correlate with these differences in
perceived appropriateness: while few participants discriminate in either treatment,
discrimination is significantly stronger between artificial groups than between
nationality groups. These results are consistent with the notion that the perceived social
appropriateness of discrimination varies according to the way identity groups are defined,
and this corresponds with individuals' revealed preferences for discrimination. That
discrimination can be observed along a trivial, artificially-induced dimension of identity
highlights the strength of the human inclination to discriminate against out-group
members, and the ease with which in-group bias can be triggered (Ashburn-Nardo et al.,
2001). That we observe weaker discrimination when identity is based upon the more
meaningful characteristic of nationality, and that such discrimination is perceived to be
more socially inappropriate, suggests that the extent to which human society has been
effective in curbing the inclination to discriminate is owing to the development of shared
norms proscribing this behaviour. Our study's main contribution is in linking
discrimination to social norms and social identity theory. In this sense, our study is
closely related to the paper by Chang et al. (2017), who investigate the effect of priming
US citizens' political identities on redistributive behaviour. They show that individuals'
primed political identities (Democrat or Republican) determine their perceptions of the
social appropriateness of redistribution, and that this explains differences in
redistributive behaviour between Democrats and Republicans. Like Chang et al.'s, our
experiment shows that both individuals' distributive decisions and their perceptions of
the social appropriateness of such decisions are sensitive to the dimension of identity
that is salient in a given context. However, while the normative prescriptions upon which
Chang et al. focus relate to the social identities of the decision-makers alone, we focus
on the social identities of both the decision-makers and other individuals affected by the
decision-makers' behaviour, and on how those social identities relate one to another.
Thus, unlike Chang et al., in our experiment both the priming and the distributive
decisions have an intergroup component which allows us to investigate the relationship
between social identities, social norms, and discriminatory behaviour. Our paper is also
related to work on the associations between social identity and norm enforcement.8
Bernhard et al. (2006) and Goette et al. (2006), for instance, use third-party punishment
games to study whether the willingness to enforce norms of sharing and cooperation depends
on the social identities of the norm violator and of the victim of the norm violation and
on how those identities relate to that of the norm enforcer. Both papers find that social
identity systematically affects the patterns of norm enforcement: enforcers are generally
more willing to mete out punishment against violators when the victim of the norm
violation is an in-group rather than an out-group member. Also related is Harris et al.
(2014), who study whether in-group favouritism is proscribed by social norms by observing
the extent to which individuals are willing to incur costs to punish it. They find that
in-group favouritism goes largely unpunished when the punisher belongs to the same
identity group as the norm violator or when she belongs to a neutral group. In-group
favouritism is instead frequently punished when the punisher belongs to a different
identity group. Harris et al. conclude that in-group favouritism is not always considered
a violation of social norms, as this depends on the identities of the agents involved in
the interaction. While these studies strongly suggest an association between
discrimination and social norms and identities, none of them has directly measured the
norms that underlie the observed patterns of behaviour. Moreover, none of these studies
has investigated whether variations in primed social identity trigger differences in norms
that, in turn, predict variations in discrimination. Thus, our study fills an important
gap in this literature, as we are the first to provide direct evidence not only that
discrimination co-varies with social norms, but also that these norms vary across
particular dimensions of an individual's identity. The rest of the paper is set out as
follows: Section 2 sketches a simple theoretical model of identity and norm-compliance
that we use to motivate and inform our empirical strategy. Section 3 outlines our
experimental design; Section 4 presents our results; Section 5 concludes and discusses our
findings.

<h>THEORETICAL FRAMEWORK</h>
---------------------

We assume that the decision-maker's utility can be broken into three components. The first
component, Vi(a), describes individual i's utility over material payoffs, which in turn
depends upon his or her own actions and the actions of others. Note that this accommodates
standard self-regarding preferences, where the individual only cares about his or her own
material payoff, as well as various forms of outcome-based other-regarding preferences,
where individual i's utility also depends on others' material payoffs (e.g. Fehr and
Schmidt, 1999; Bolton and Ockenfels, 2000). Importantly, this component of utility does
not depend on the identities of the decision-maker or the others. In contrast, we assume
that the second and third components of utility depend on social identities. These capture
the decision-maker's willingness to treat others differently depending on how those
others' identities compare to his or her own identity. There are several psychological
mechanisms that form the basis for these components. Social identity theory (Tajfel and
Turner, 1979), for example, posits that discrimination helps individuals satisfy their
need for positive self-esteem since it confers a relatively high status on the in-group at
the expense of the out-group. Subjective uncertainty reduction theory (Hogg, 2000) takes a
different approach: individuals strive to reduce uncertainty about their attitudes,
beliefs, and perceptions. Self-categorization and identification with groups that provide
normative prescriptions for behaviour can reduce this uncertainty and lead to differential
treatment of in-groups and out-groups. We view these psychological mechanisms as distal
motivations for the ‘taste for discrimination’ that has been discussed in the economics
literature. In our model we operationalise these mechanisms using two distinct components
of utility. The component Si(a| I) captures what has traditionally been thought of as the
taste for discrimination, i.e. utility derived by individual i from i's and others'
material payoffs that is conditional on how the social identities of individual i and the
others relate, one to another. In our model, this component of utility can be thought of
as primal – as the direct utility that is or would be derived from favouring the in-group
in the absence of any self-moderation. As in the utility functions proposed by McLeish and
Oxoby (2007), Chen and Li (2009), and Chen and Chen (2011), this component of utility is
not conditional on which specific dimension of identity is salient in the decision-making
environment. Rather, we simply assume that i places a higher weight on the material
payoffs of those players who are in-group, i.e., have the same social identity as him- or
herself, as compared to the payoffs of players who are out-group, i.e., have a different
identity.9 This can accommodate simple forms of favouritism towards the in-group, such as
in-group altruism, as well as more complex forms of identity-contingent other-regarding
preferences, as in the models by Chen and Li (2009) and Chen and Chen (2011). The third
component of utility in our model, γiN(ai| I, d), captures the decision-maker's preference
to self-moderate his or her primal inclination to favour the in-group with reference to
what is or is not socially appropriate. Specifically, we assume that the individual
derives utility from complying with normative prescriptions, captured by the function
N(.), which defines the social appropriateness of each action ai available to individual
i. These normative prescriptions depend on social identities. They may, for example,
prescribe different behaviours towards in-group and out-group others. In addition, these
prescriptions depend on the dimension of social identity, d, that is salient given the
decision-making context. So, the same action may be viewed as more or less socially
appropriate depending not only on how the identities of the decision-maker and others
compare, but also on what dimension of identity it is appropriate or meaningful to compare
given the context. In some contexts, this third term mitigates the second. For example, an
individual might have a primal desire to direct mildly insulting comments at members of an
ethnic group other than his or her own, but refrains from doing so because it is socially
inappropriate. In other contexts, this third term may build on the second. For example, an
individual might have a primal desire to direct mildly insulting comments at the
supporters of a soccer team other than the one he or she supports and is further motivated
to do so because, especially on match days, such behaviour is socially appropriate.
Finally, γi is an individual-specific parameter defining the importance that individual i
attaches to complying with social norms. In our experiment, subjects face a simple
allocation task (described in detail in the next section), where they have to divide an
amount of money between two other participants. In all treatments of the experiment, we
keep constant the set of material payoffs available to players and the mapping from
actions into payoffs. Thus, the first component Vi(a) of the utility function above is
held constant across treatments for any given set of actions a. Moreover, in all
treatments subjects are asked to divide the money between a participant who belongs to the
same identity group as themselves and a participant who belongs to a different identity
group. Thus, the second component Si(a| I) of the utility function is also kept constant
across treatments. Our treatments vary the dimension of identity d that is made salient to
the decision-makers and, hence, the process by which the relevant identity groups are
defined in the experiment. As we describe in detail in the next section, in one treatment
identity groups are formed on the basis of a random event, while in the other treatment
identity groups are based on a meaningful personal characteristic. An implication of this
treatment manipulation is that the normative prescriptions, N(ai| I, d), that regulate the
third component of the utility function described above, may differ across treatments.
Specifically, the same action ai available to the decision-maker may be evaluated
differently depending on how identity groups are formed. Our experiment empirically
explores the effect of varying the salient dimension of identity on the normative
prescriptions relating to discriminatory behaviour and the role of these normative
prescriptions in predicting such behaviour. Note that our model does not specify ex-ante
the underlying determinants of the perceptions of appropriate behaviour captured by the
function N(.), or how these will vary across treatments. Instead, we follow Krupka and
Weber (2013) and Chang et al. (2017) and employ a norm-elicitation technique to quantify,
in an incentive-compatible way, the function N(.) in each treatment.10 This allows us to
assess empirically the extent to which normative prescriptions do indeed differ across
treatments; and thereby examine the extent to which differences between treatments in the
level of discrimination in the allocation task are predicted by differences in the
perception of its appropriateness.

<hs>  Measuring discrimination – the allocator game</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In the allocator game, one participant was endowed with £16 and asked to allocate it
between two passive players, one belonging to his or her own identity group and the other
belonging to a different identity group.11 The decision-maker could not keep any of the
money for him- or herself but knew he or she would receive a payment, between £6 and £10,
which the computer would randomly pick at the end of the experiment.12 Allocators could
split the money any way they liked between the other two players, as long as each amount
was a multiple of two. Thus, the allocator had to choose one of nine possible allocations
of money between the two passive players, ranging from (£16; £0) to (£0; £16). In order to
maximize sample sizes, we elicited decisions using a role randomisation method: all
participants were asked to make a decision in the allocator role knowing that their actual
role would be determined at random at the end of the experiment (participants had a one-
third chance of being assigned the allocator role and a two-thirds chance of being
assigned a passive player role). Role assignment was implemented at the end of experiment,
once everyone had submitted an allocation decision. Decisions were made anonymously and
the only information allocators had about their recipients was the identity group that
each of them belonged to. We chose the allocator game as our discrimination-eliciting
device for the following reasons. First, given our focus on taste-based discrimination, we
wanted a decision-making task within which statistical discrimination had no relevance; in
the allocator game the decision-maker's material payoff does not depend on what any other
player does, so statistical beliefs about other players are irrelevant.13 Second, to
maximize our chances of discerning treatment differences, we wanted a task that reliably
produces discriminatory behaviour and, in a meta-analysis, Lane (2016) found the allocator
game to be the experimental task that yielded the strongest discrimination. Finally, in
the allocator game it is obvious to participants what the experiment is about and any
observed discrimination is interpretable as conscious rather than subconscious. Thus, the
game is an ideal subject for a norm-elicitation task; it is much simpler to assess the
social appropriateness of conscious behaviour than of subconscious behaviour.

<hs>  Measuring the social appropriateness of discrimination – the Krupka-Weber norm-elicitation task</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We elicited the social appropriateness of discrimination in the allocator game using an
adaptation of the task design pioneered by Krupka and Weber (2013). Participants were
described the allocator game, were presented with a table listing the nine possible
actions an allocator could take, and were asked to evaluate the social appropriateness of
each by selecting one option on a four-point scale: ‘Very socially inappropriate’,
‘Somewhat socially inappropriate’, ‘Somewhat socially appropriate’ or ‘Very socially
appropriate.’ To ensure that the relevant perceptions of appropriateness are measured, the
evaluators should be, to the greatest extent possible, in the mind-set of the person
making the decision they are evaluating. In our experiment, in contrast to the original
Krupka and Weber method, participants in the norm-elicitation task were the same as those
playing the allocator game. This allows us to look at within-individual correlations
between norms and actions. To facilitate an investigation into whether this had
implications for either the behavioural or normative data, we varied which task came first
(participants were unaware of the content of the second task until they had completed the
first).14 All participants were assigned to identity groups before their first task, so
those taking the norm-elicitation task first had had their identities primed in exactly
the same way as the allocator game participants whose behaviour they were evaluating. Each
individual in the norm-elicitation task only evaluated the appropriateness of actions made
by allocators of the same identity group. The evaluation of actions was incentivised.
Participants were told that, at the end of the experiment, one of the nine actions they
had evaluated would be randomly selected, and each participant's evaluation of the action
would be compared to that of another randomly selected participant. If a participant's
evaluation matched that of the person they were compared with, that participant would earn
£8; otherwise they would earn nothing. These incentives transform the task into a
coordination game, where participants are incentivised to match other participants'
evaluations of appropriateness. Krupka and Weber (2013) argue that this gives participants
an incentive to reveal their perception of what is commonly regarded as appropriate or
inappropriate behaviour in the decision situation, rather than their own personal
evaluation of the actions they are asked to consider. This is important because social
norms are collectively recognised rules of behaviour, rather than personal opinions about
behaviours (e.g. Elster, 1989; Ostrom, 2000). Moreover, because we wanted to incentivise
participants to coordinate on identity-specific social norms (i.e. the social norms that
were recognised by those belonging to a specific identity group), participants were told
that the person whose evaluation theirs would be compared to would be a member of their
own identity group. Participants were told: ‘By socially appropriate, we mean behaviour
that you think most participants [of your group] would agree is the “correct” thing to do.
Another way to think about what we mean is that if [the allocator] were to select a
socially inappropriate action, then another participant [of your group] might be angry at
[the allocator].’

<hs>  Treatments</hs>
  ~~~~~~~~~~

Our treatments, labelled Nationality and Artificial, differed in the way identity groups
were formed. In Nationality participants in the experiment were segregated into identity
groups based on nationality (previous economics studies taking this approach include
Netzer and Sutter, 2009; Guillen and Ji, 2011; Goerg et al., 2016). In Artificial
participants were split into ‘minimal groups’, using a variant of the technique first
introduced by Tajfel et al. (1971), wherein social identities are artificially instilled
in participants during the experiment. For both treatments we recruited British and
Chinese students at the UK campus of the University of Nottingham, a British institution
which hosts a large number of students from China.15 In the Nationality treatment, upon
arrival, the British were seated on one side of the lab and the Chinese on the other. At
every computer terminal on the British (Chinese) side was placed a sign reading ‘YOU ARE
ON THE BRITISH (CHINESE) SIDE OF THE ROOM. ALL PARTICIPANTS ON THIS SIDE OF THE ROOM ARE
BRITISH (CHINESE)’ (see Supplementary Online Materials B). In the instructions at the
beginning of the experiment, it was again made explicitly clear that the lab and the
participants had been divided based on nationality. In the Artificial treatment, upon
arrival, participants blindly drew a ball from a bag. In each session the bag initially
contained equal numbers of green and yellow balls, and participants continued to draw from
it until the bag was empty, thus ensuring an equal split of green and yellow balls drawn.
Those with green balls were then seated on one side of the lab, and those with yellow on
the other. Consistent with the Nationality treatment, signs were placed at each terminal,
reading ‘YOU ARE ON THE GREEN (YELLOW) SIDE OF THE ROOM. ALL PARTICIPANTS ON THIS SIDE OF
THE ROOM DREW A GREEN (YELLOW) BALL’, and it was again made explicit at the beginning of
the instructions that the lab and the participants had been divided on the basis of ball
colour. As in the Nationality treatment, we invited an equal mix of British and Chinese
students to the Artificial sessions. This ensures comparability between the two
treatments.16 We conjectured that the normative prescriptions regulating the third
component of utility in Eq. (1) would differ across the two treatments. Specifically, we
conjectured that favouring the in-group at the expense of the out-group would be viewed as
less appropriate in the Nationality compared to the Artificial treatment. This specific
conjecture was derived from the following assumptions and observations. First, we
considered the Nationality treatment. In Britain, a liberal society with a long history of
in-migration, it seemed reasonable to assume: first, the existence of a norm proscribing
discrimination against people from nations other than one's own; and second, that both the
British and the Chinese participants in our experiment recognised such a norm and its
relevance under the Nationality treatment. Under these assumptions, the third component of
utility in Eq. (1) is discrimination prohibiting. Second, we considered the Artificial
treatment. In this case, there was no directly relevant social norm to which participants
could refer. However, we conjectured that participants could have referred to one or more
apparently partially relevant social prescriptions or norms.17 So for some, the specifics
of the Artificial treatment could have brought to mind dimensions of identity such as
nationality or ethnicity. However, it seemed reasonable to assume that for others it would
have been more likely to invoke dimensions of identity such as sports fandom and team
game-playing, across which discrimination is condoned. Thus, we conjectured that, under
Artificial, to the extent that any normative prescription or prescriptions were regulating
the third component of utility in Eq. (1), on average, they would be less discrimination
prohibiting than those at work under Nationality. Finally, we noted that this conjecture
is consistent with the fact that previous experiments priming national identity (e.g.
Goerg et al., 2016; Netzer and Sutter, 2009; Willinger et al., 2003) have often not found
significant discrimination, while experiments involving minimal group identity (e.g.,
Ahmed, 2007; Chen and Li, 2009; Hargreaves Heap and Zizzo, 2009) do so more frequently.18
Indeed, according to a recent meta-analysis by Lane (2016), on average, discrimination is
significantly weaker in the former compared to the latter type of experiment.

<hs>  Procedure</hs>
  ~~~~~~~~~

All participants participated in both the allocator game and the norm-elicitation task, as
well as completing a post-experimental questionnaire. In each session, everyone received
payment either for the allocator game or for the norm-elicitation task, as determined by a
coin toss at the end of the experiment. Participants also received a £4 show-up fee. The
order in which the tasks were performed was randomised between sessions, so that we could
check for ordering effects. We do not find such effects (see Supplementary Online
Materials C for the analysis), which is consistent with the findings of Erkut et al.
(2015) and D'Adda et al. (2016). Therefore, in the analysis below we pool across ordering
conditions. All sessions had 24 participants – twelve belonging to each group – and were
conducted in March or April 2015, using z-Tree (Fischbacher, 2007). We conducted ten
sessions, with 120 participants participating in each treatment.19

<hs>  Treatment differences – social norms</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We look first at the social appropriateness of discrimination in each treatment, as
measured by the norm-elicitation task. Fig. 3 plots the mean appropriateness ratings
assigned to each allocation in the Nationality and Artificial treatments. Following the
approach of Krupka and Weber (2013), we assign evenly-spaced values of −1 for the rating
‘very socially inappropriate’, −0.33 for the rating ‘somewhat socially inappropriate’,
0.33 for the rating ‘somewhat socially appropriate’ and 1 for the rating ‘very socially
appropriate.’ The table at the bottom of the figure displays the distribution of
evaluations for each allocation in each treatment, and presents the results of
randomisation tests on the treatment differences in mean ratings. Our results are
corrected for the fact that we are performing multiple tests; applying the Benjamini-
Hochberg False Discovery Rate method (Benjamini and Hochberg, 1995), we sort our p-values
in ascending rank and multiply each by the number of separate tests being performed (in
our case nine, one for each possible allocation) before dividing each by its rank – thus
greater adjustments are made to smaller p-values.20 In each treatment the mean and modal
evaluations follow the same general pattern. Participants tend to regard extreme
discrimination against recipients belonging to either identity group to be very socially
inappropriate, while the equal split is generally regarded as very socially appropriate.
There is a lack of strong consensus on allocations mildly favouring members of one group
or the other. This pattern is consistent with a social norm of equality. However, in both
treatments the perceived social appropriateness decays faster as allocations move away
from equality towards favouring the out-group member than when they move towards favouring
the in-group member, indicating that social norms against discrimination are stronger when
the victim is a member of one's own identity group.21 By design, any treatment differences
in the ratings assigned to a given allocation can only be driven by contextual differences
in the perceived appropriateness of discrimination. We observe subtle but significant
treatment differences. Whereas 95% of participants in the Nationality treatment perceive
the equal split to be very appropriate, the equivalent figure is only 84.2% in the
Artificial treatment; mean ratings for the equal split are significantly higher in the
Nationality treatment. Furthermore, as the allocations move away from the equal split
towards favouring the in-group, the appropriateness ratings decline at a faster rate in
the Nationality treatment than in the Artificial treatment. For the extreme (16,0) split,
92.5% of participants in the Nationality treatment opt for ‘very inappropriate’, while
only 80.8% do so in the Artificial treatment. And while only 5% of participants rate the
(16,0) allocation as socially appropriate in the Nationality treatment, 18% do so in the
Artificial treatment. In fact, Fig. 3 shows that, for any in-group-favouring allocation,
there are more participants in the Artificial than Nationality treatment who find
discrimination to be socially appropriate.22 As a consequence, all in-group-favouring
allocations are, on average, perceived to be more appropriate in the Artificial treatment,
and the differences are statistically significant at the 5% level or better in three out
of the four possible cases (the exception being the allocation 14, 2 for which the
difference is significant at the 10% level). Moreover, the differences in perception of
appropriateness of discrimination only pertain to in-group favouritism and not to any form
of discrimination; Fig. 3 shows that, while out-group-favouring allocations are, on
average, perceived to be slightly more appropriate in the Artificial treatment, only for
the (6,10) allocation is the difference significant, and then only at the 10% level.23

<hs>  Treatment differences – discrimination</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Fig. 4 presents the distribution of decisions made in the allocator game in each
treatment. In the Nationality treatment, 83.3% of participants choose to allocate the
money evenly between the in-group member and the out-group member. Only 69.2% of the
participants in the Artificial treatment make this choice. The remainder of participants
in each treatment discriminate against out-group members; no participant in either
treatment allocates more money to the out-group member than the in-group member. 12.5% of
participants in the Artificial treatment allocate all the money to the in-group member,
while only 4.2% do so in the Nationality treatment. In the Nationality treatment,
participants allocate an average of £8.67 to the in-group member and £7.33 to the out-
group member, resulting in a mean difference of £1.33. In the Artificial treatment,
participants allocate an average of £9.52 to the in-group member and £6.48 to the out-
group member, resulting in a mean difference of £3.03. A randomisation test indicates that
the mean difference in the Artificial treatment is significantly higher than that in the
Nationality treatment (p = 0.007). This is consistent with the conjecture that
discrimination is stronger in the treatment where it is perceived to be more socially
appropriate. It suggests that norm-compliance moderates discriminatory behaviour.24 In
Table 1, an OLS regression confirms that the treatment effect on discrimination is robust
to the inclusion of various controls – such as age, gender, nationality and the extent to
which participants understand the tasks.25,26

<hs>  Econometric analysis of individual perceptions of social appropriateness and behaviour</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

So far we have analysed the link between behaviour and norms at the group level, by
showing that there is more discrimination in the treatment where it is perceived as less
socially inappropriate. We now exploit the within-subject nature of our experiment to
extend the analysis to the individual level. Specifically, we investigate whether a model
that incorporates a preference for norm compliance is better able to explain the
behavioural regularities in our experiment than a model that does not incorporate such a
factor. Following the theoretical framework introduced in Section 2, we assume that the
utility that allocators derive from choosing allocation x depends on three components,
defined respectively on material payoffs, identity-contingent preferences over material
payoffs, and normative prescriptions. We assume that the first component depends on the
squared difference between the material payoffs of the two passive players implied by
allocation x. The parameter v captures the weight that the allocator places on the
material payoff component of the utility function, regardless of the identities of the
passive players: allocations that implement unequal payoffs carry the same weight to
utility, regardless of whether the inequality favours the in-group or out-group. Thus, the
parameter v simply captures (identity-blind) preferences associated with payoff
inequality. In contrast, the parameters s and γ capture the weight that the allocator
places on the components of utility that are contingent on the identities of the passive
players. The parameter s captures simple in-group altruism: the allocator places an extra
weight on the material payoff of the passive player who belongs to the same group as him-
or herself (and zero weight on the payoff of the out-group). Finally, the parameter γ
captures the weight that allocators place on (identity-related) normative prescriptions.
Our objective, here, is to show that a norm-augmented model is better able to capture the
data patterns observed in the experiment than a model which contains only the first two
components of utility captured in Eq. (2) above. Thus, in Table 2 we report the output of
two fixed-effects conditional logit models, each estimated using all of the allocation
decisions and, in Model (B), all of the social appropriateness evaluations generated under
either the Nationality or the Artificial treatment. In the first model we impose the
restriction γ = 0 to the utility function in Eq. (2) and, thus, estimate a choice model
where the decision-maker is purely concerned with payoff inequality and simple in-group
altruism. In the second model this restriction is removed and utility is allowed to depend
on payoff inequality, simple in-group altruism, and the individual's normative evaluation
of the action under consideration. The significant negative estimates of v in both models
indicate that actions which yield larger payoff inequalities are less likely to be chosen.
The estimate of s is positive and significant in both models, indicating that allocations
which favour the in-group are more likely to be chosen. Finally, the significant positive
estimate of γ in model (B) indicates that an individual is more likely to choose actions
he or she perceives to be more socially appropriate. The significant estimate of γ in a
model that also includes the v and s parameters indicates that the normative component of
the utility function can explain variation in choice behaviour that cannot be entirely
captured by (identity-blind) inequality considerations combined with simple in-group
altruism. This also explains why the Bayesian Information Criterion is significantly lower
for model (B) than (A) (p < 0.001 on a likelihood-ratio test) indicating that the norm-
augmented model fits the data significantly better than the model without norms. The
reason why the norm-augmented model performs better is made clear in Fig. 5, in which the
aggregate action choice rates predicted by each of the models are graphed next to the
actual choice rates (as displayed in Fig. 4). The left-hand panel of Fig. 5 presents the
choice rates predicted by model (A). The right-hand panel presents the choice rates
predicted by model (B). For ease of comparison, actual choice rates are reproduced in both
panels. In each panel, the predicted choice rates (striped bars) and actual choice rates
(shaded bars) of the Nationality (Artificial) treatment are shown in dark (light) grey.
Model (A), in which participants care only about inequality and in-group altruism,
captures some important aspects of the choice data. In particular, the model predicts that
deviations from equality are asymmetric across the choice space. That is, the probability
of choosing an unequal and in-group-favouring allocation is predicted to be higher than
that of choosing an allocation which creates the same payoff inequality but favours the
out-group. This is what we observe in the actual choice data, as no-one chooses out-group-
favouring allocations, while 24% of participants choose an in-group-favouring allocation.
However, Model (A) fails to capture a second key feature of the choice data, the
difference in allocations across treatments. In contrast, the norm-augmented model (B)
predicts a lower probability of choosing the equal split allocation and higher
probabilities of choosing in-group-favouring allocations in the Artificial compared to the
Nationality treatment. This is in line with what we observed in the experiment. Moreover,
although the model still assigns positive probabilities to out-group-favouring
allocations, they are markedly lower than those predicted by Model (A). Before concluding,
we need to investigate whether identity-contingent preferences over material payoffs
(captured by the term s[∥Ii=Ijπj(ax) + ∥Ii=Ikπk(ax)] in Eq. (2)) depend on the dimension
of social identity that is salient in the decision-making situation. We would expect to
observe such a dependence if, for example, in-group altruism varies depending on how
strongly individuals identify with the group and this, in turn, depends on the dimension
of identity along which groups are defined. Here, as in Model (B) in Table 2, v is highly
significant and negative and both γ and s are highly significant and positive, while the
newly added σ is statistically insignificant.28 Thus, we cannot reject the null hypothesis
that direct utility derived from in-group altruism is independent of the dimension of
social identity that is salient in the decision-making situation, and retain Eq. (2) as
our preferred specification of utility.

<h>CONCLUSION</h>
----------

We show that discrimination is perceived to be socially inappropriate. However, the extent
of this perceived inappropriateness depends on the identities upon which discrimination is
based: when the identities are defined with reference to a brief, random event,
discrimination in favour of the in-group is viewed as less inappropriate than when the
identities are based on nationality. Furthermore, we show that discrimination in the
allocator game is stronger in the setting where it is perceived to be less inappropriate,
and that, at the individual level, perceived inappropriateness predicts actual behaviour.
Our findings are supportive of a theoretical framework within which taste-based
discrimination is partly driven by normative considerations about the appropriateness of
discriminatory behaviour. We offer direct evidence that, across choice contexts that are
otherwise identical, differences in the way identity groups are defined translate into
differences in the perceived normative prescriptions, and corresponding differences in
behaviour towards in-group and out-group members. These findings are in line with models
of social identity that have emphasised the role of social norms, such as Akerlof and
Kranton (2000, 2005). Consistent with longstanding results from the minimal group
literature, our study shows how remarkably easy it is to trigger discrimination between
groups whose identities are based on artificial, trivial characteristics. That we find
weaker discrimination on the basis of more meaningful identity characteristics such as
nationalities, and that discrimination is perceived to be more socially inappropriate in
that setting, suggests that shared norms opposing discrimination help moderate this most
natural of human inclinations. We remain agnostic as to exactly why these norms opposing
discrimination are more strongly triggered by national identity than by minimal group
identity. National groups are different from minimal groups in various ways, so there are
multiple possible explanations. We conjecture that a norm proscribing discrimination on
the basis of nationality is likely to have developed over time in a liberal society, with
a long history of in-migration, such as Britain, perhaps enhanced by sensitivities about
the negative historical effects of racism and xenophobia. For these reasons, grouping
participants by nationality seems likely to invoke stronger norms against discrimination
than if we grouped them by other types of natural identity, such as university affiliation
(as implemented, for instance, in Ockenfels and Werner, 2014). In the case of minimal
groups, while their members have no directly relevant norms to refer to, we argue that
they are relatively likely to invoke types of identity such as sports fandom and team
game-playing, across which discrimination is considered harmless. It is also possible that
some participants under minimal group identity perceive that the experimenter intends for
them to discriminate, and that this experimental demand leads them to perceive a social
norm in favour of discrimination. These are matters for interesting future research. While
further investigation is needed, our findings are consistent with and strongly suggest
that shared norms opposing discrimination do, as one would expect, help moderate
discrimination. One likely implication of this would be that if society allows such
prohibitive social norms to be eroded by whatever means, discrimination will increase.
This would be consistent with the recent co-emergence of a backlash in various western
countries against ‘political correctness’, spurred on by leaders promoting nationalism and
identity politics, and the apparent rise in hostility towards immigrants and ethnic
minorities in these countries.


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<ART>Ownership of intellectual property and corporate taxation
=========================================================

Authors: Rachel Griffith, Helen Miller, Martin O'Connell
DOI: 10.1016/j.jpubeco.2014.01.009
Year: 2014  |  Pages: 12-23
ASJC codes: 2002, 2003
Keywords: Corporate tax, Intellectual property, Multinational firms, Patent Boxes

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Intellectual property accounts for a growing share of firms' assets. It is more mobile than other forms of capital, and could be used by firms to shift income offshore and to reduce their corporate income tax liability. We consider how influential corporate income taxes are in determining where firms choose to legally own intellectual property. We estimate a mixed (or random coefficients) logit model that incorporates important observed and unobserved heterogeneity in firms' location choices. We obtain estimates of the full set of location specific tax elasticities and conduct ex ante analysis of how the location of ownership of intellectual property will respond to changes in tax policy. We find that recent reforms that give preferential tax treatment to income arising from patents are likely to have significant effects on the location of ownership of new intellectual property, and could lead to substantial reductions in tax revenue. © 2014.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The growing importance of intellectual property as a factor in production,1 and concern
that it is easier for firms to shift income from this source than it is from others,
presents challenges for tax design. Firms can and do position their intellectual property
with a view to reducing tax liabilities. However, despite these concerns, firms do not by
and large locate the legal ownership of intellectual property in the lowest tax countries,
and corporate income taxes still raise considerable amounts of revenue in most developed
countries. In this paper we address the question of how influential corporate income taxes
are in determining where firms choose to legally register ownership of an important form
of intangible assets, patents. Our contribution is to extend the empirical literature on
public policy and firm location choice by introducing new methods to this area of public
economics. We estimate a mixed (or random coefficients) logit model that incorporates both
observed and unobserved heterogeneity in firms' location choices (see inter alia, Berry et
al. (1995, 2004), Nevo (2001) and Train (2003)). A key strength of this approach is that
it allows us to compute own and cross tax elasticities across locations that reflect
patterns of correlation in observed choices in the data, and therefore to capture more
realistic substitution patterns than standard logit models. Our estimates allow us to
conduct ex ante analysis of how the location of ownership of intellectual property will
respond to changes in policy. We use our estimates to simulate responses to recent policy
reforms that provide preferential tax treatment to income arising from patents. We find
that these reforms are likely to have significant effects on the location of ownership of
new intellectual property, and could lead to substantial reductions in tax revenue. Our
estimates could be used to simulate a wide range of other counterfactual situations. We
use comprehensive panel data on all patent applications made to the European Patent Office
(EPO) by a large number of innovative European firms over 1985–2005. A patent is a legal
document that grants a firm the exclusive rights to use or licence a novel technology for
a specified period of time. A firm can register legal ownership of a patent in a
subsidiary that is located in a country different to the firm's headquarters, different to
the location where the underlying technology was created and different to the location
where the intellectual property will be applied. Lipsey (2010) notes that, in
multinational firms, intangible assets “have no clear geographical location, but only a
nominal location determined by the parent company's tax or legal strategies.” For example,
Fig. 1 shows the share of patent applications made by UK parent firms where the legal
ownership is registered outside of the UK and in a separate place to where the underlying
innovative activity occurred. This share has increased six-fold over the past two decades.
The largest proportion has gone to countries that have a lower tax rate than the UK, but
the amount going to countries with a higher tax rate has also increased. We model the
impact of tax on where firms choose to locate the legal ownership of patents. Tax could
influence this decision because the legal ownership of the patent will be one of the
determinants of where the income derived from the patent is taxed. The profits earned from
the exploitation of intellectual property will be the result of a number of activities,
including the research and development (R&D) investment undertaken to create the new idea,
the financing of this investment and the subsequent commercialisation. When these
activities take place in multiple countries, as is often the case for multinational firms,
the returns must be allocated to individual jurisdictions for tax purposes. Firms have an
incentive to arrange their activities in such a way that, all else equal, profits accrue
in the country in which they would pay the lowest tax. There are a number of strategies
that can be used to achieve this. Such strategies commonly require that the income earned
from exploiting intellectual property accrues outside of the country in which the
underlying R&D took place. One way to achieve this is through contract R&D. For example, a
subsidiary in a relatively low tax country may finance (and bear the risk for) R&D
activities that are contracted to a related subsidiary in a higher tax country (possibly
with the benefit of R&D tax incentives and access to high skills levels). The contract
will specify the payment to be made for the R&D activities (commonly equal to the costs
incurred plus an arm's length mark-up). Returns above this payment, either from using the
technology directly or from licensing it, will accrue to the subsidiary that bore the
financial risk. There is a tax advantage to this strategy if the true value of the R&D
activities is less than the price paid for the contract R&D. A similar result may be
achieved through the use of a cost sharing agreement that specifies how subsidiaries will
share the costs, risks and returns associated with an R&D project. Such agreements may be
designed such that the right to exploit and capture the returns from a technology accrues
to a subsidiary in a low tax country. The strategies available to a firm depend on how the
firm is organised and on the precise tax rules they are subject to (Finnerty et al.
(2007)). Tax rules limit a firm's ability to manipulate where income arises for tax
purposes. Shifting income typically requires that payments made to compensate the company
that conducts the R&D, or royalties made for the use of a technology, are at preferential
prices. There are transfer pricing rules that aim to enforce the principle that the prices
of intra-firm transactions are set as if they had occurred between unrelated parties —
this is the arm's length principle. However, these transactions often do not have market
counterparts, which means that firms may have opportunities to set the prices of related
transactions in such a way as to reduce tax liability.2 Tax rules, including those that
dictate how a firm can allocate the returns to innovative activities, differ across
European countries and are different to those faced by US multinationals. For example,
countries differ on the acceptable methods used to calculate payments for contracted R&D
services, and where there are cost sharing agreements, countries differ in the
requirements over whether all subsidiaries involved in the agreement need be engaged in
R&D (in contrast to the US, not all European countries allow holding companies in low tax
locations to be part of cost sharing agreements). The corporate tax rate is likely to be
an important determinant of the location in which a firm chooses to hold legal ownership
of intellectual property. However, it is unlikely to be the only factor; we would not
expect all intellectual property to be legally registered in the lowest tax countries.
Indeed, legal ownership of patents is rarely in the set of small countries that are often
considered to be tax havens. The patents that are legally owned in such countries
accounted for fewer than 0.5% of all patent applications made to the European Patent
Office over the period 2001–2005, and many of those are unrelated to European firms.3 This
could be due, at least in part, to the operation of Controlled Foreign Company (CFC)
regimes, which effectively seeks to tax income at the higher home country tax rate if it
is deemed to be located in a low tax country for tax purposes. More generally, there may
be characteristics of a location over and above its corporate tax rate that firms value.
For example, the strength of intellectual property rights protection and market size might
play a role, and, all else equal, firms may be more likely to co-locate ownership of
intellectual property with associated real innovative activity due to externalities from
co-location. There is likely to be a large degree of heterogeneity in how responsive firms
are to tax when deciding where to locate the legal ownership of their intellectual
property; a number of papers have emphasised the importance of incorporating heterogeneity
in firms' decisions (Melitz (2003), Bernard et al. (2007a, 2007b), Krautheim and Schmidt-
Eisenlohr (2011)). This heterogeneity will arise for a number of reasons, some of which
relate to observable factors, and others that relate to factors unobserved by the
econometrician. For example, firms are likely to be more sensitive to tax when choosing
the location in which to legally own patents with a relatively high expected value (Becker
and Fuest (2007), Bohm et al. (2012)). Firms are also likely to be differentially
responsive to tax due to differences in their organisational structures. Their existing
network of subsidiaries, the proficiency of their tax department and the tax strategies
they are able to employ for managing income from intellectual property will play a role.
Firms with headquarters in different countries might respond differently if countries
differ in the stringency of their tax rules and in the effectiveness with which they are
applied. Firms operating in some markets or using certain technologies might respond
differently, because, for example, transfer pricing rules may be easier to circumvent for
firms operating in markets where a high share of transactions are intra-firm meaning it is
difficult for tax authorities to accurately assess what is a fair market price. Both firm
size and industry have been highlighted as important in the context of firm decision
making over how to organise offshore activities (Graham and Tucker (2006) and Desai et al.
(2006)). Indeed, the value of a patent, the relative attractiveness of a location and a
firm's strategies and organisational structures are likely to vary across industries and,
within industries, across firms. Our work relates to several papers in the literature.
Most closely related, Dischinger and Riedel (2011) and Karkinsky and Riedel (2012)
estimate the relationship between corporate tax and, respectively, the quantity of
intangible assets and the number of patent applications made by subsidiaries located in
each of a number of European countries. Also related is Ernst and Spengel (2011) who
estimate the impact of R&D tax incentives and corporate tax on patenting. In common with
these papers, we are interested in the relationship between corporate tax and where firms
choose to locate intellectual property. We extend this literature by estimating a choice
model that allows us to compute the full set of own tax and cross tax elasticities and
which allows us to carry out ex ante analysis of how location decisions will respond to
potential policy changes. Our work is also related to Cohen (2012), which uses a discrete
choice framework to study how the design of US state tax rules influence US firms'
decisions over in which state to incorporate. There is a considerable literature in the
Hall and Jorgenson (1967) tradition that considers the impact of taxes on production
activity and on the location of R&D. Hines (1996, 1999) and Devereux (2006) provide
surveys of the empirical literature. This literature finds that, despite the many factors
that will influence a firm's location decision, tax exerts a significant effect on
location choices. Hines and Jaffe (2001) show that tax affects the location of firms'
innovative activities within US multinational groups. Most relevant for our analysis,
previous work has highlighted the role that intangible assets play in allowing firms to
organise their activities with a view to reducing their tax burden (Altshuler and Grubert
(2006)). Empirical studies provide indirect evidence of tax avoidance by, for example
showing that firms have relatively high profitability in low tax countries (Grubert and
Mutti (1991), Hines and Rice (1994)) and that the share of royalty payments associated
with low tax countries is higher than expected (Grubert and Mutti (2009)). Grubert (2003)
formalises how intangible assets can be used to shift income and finds that about half of
the income shifted from high-tax to low-tax countries by US manufacturing firms can be
accounted for by income from R&D linked intangibles. The structure of the paper is as
follows. In Section 2 we outline a model of a firm's decision over where to locate the
legal ownership of a patent. In Section 3 we describe the data we use to estimate the
model. Section 4 presents the estimated coefficients and the tax elasticities between
locations. An example of how the model can be used to conduct policy simulations is given
in Section 5, where we consider the impact of recent reforms that reduce the tax rate for
income derived from patents. A final section summarises and concludes.

<h>FIRM BEHAVIOUR</h>
--------------

When a firm generates a new idea, it expects to earn a stream of income on the application
of that idea in the future. Ideas will vary both in their expected values and in the
number of patents they give rise to (some will lead to one patent and some will lead to
many). A firm faces the decision over where to initially locate the legal ownership of
each patent. It will make this decision based, in part, on the rate of tax that it expects
to face on income generated by the use of the patent in the future. Unobserved attributes
of ideas are likely to be crucial, and potentially could generate correlations in patent
location decisions. The firm will also take account of other characteristics of locations
that it may value, for example, whether the real innovative activity associated with that
intellectual property is also located there, the potential size of the market (if it also
expects to commercialise the idea in that location), intellectual property rights'
protection, technological condition, and many other location specific factors, at least
some of which are likely to be unobserved by the econometrician. The importance of these
location characteristic are likely to vary across ideas. For example, high value ideas may
be more tax sensitive and the importance of intellectual property protection may differ
across industries. We develop a tractable empirical model that captures these determinants
of location choice.

<hs>  Firm payoffs</hs>
  ~~~~~~~~~~~~

We specify a model in which a parent firm decides where to locate the legal ownership of
each of its patents. Firms, indexed f = 1,…,F, realise ideas, indexed i = 1,…,I. Ideas are
assumed to arise exogenously over time, indexed t. Each idea can yield a single patent or
a group of related patents; patents are indexed p = 1,…,P. We model the country, indexed j
= 1,…,J, in which the parent firm decides to locate the legal ownership of each patent,
allowing for correlation in decisions between related patents (those that are part of the
same idea). We consider all patents taken out by a parent firm that are technologically
related in a quarter as part of the same idea; the precise definition of an idea is given
in Section 1. For each patent, the parent firm chooses the location that yields the
highest payoff. The payoff the parent firm gets from choosing a location depends on the
tax rate it expects to face, τfjt, the quality of the idea, qi, whether any research
activity that gave rise to the idea is located there, aijt, the strength of the country's
intellectual property rights protection, the size of the local market (measured as GDP),
and the level of technological innovativeness (measured as total annual business R&D
expenditure as a share of GDP), captured in the vector xjt. Crucially, we also allow
location choice to depend on unobserved characteristics of both the idea and the location.
We allow the impact of all observed and unobserved factors to vary across medium and large
firms and for technologies in different industries; the subscript r = 1,…,R denotes the
industry–firm size category an idea belongs to. The tax rate τfjt varies across firms,
because the tax system in a firm's residence jurisdiction may interact with the rules of
the countries in which it is considering locating ownership of a patent through the
operation of Controlled Foreign Company (CFC) rules. We use the tax rate dated t, making
the assumption that when a firm chooses the location of a patent it expects that the
current tax regime will apply in the future. The tax parameter, αi, is at the idea level.
We allow it to vary with an observed measure of idea quality, qi. Patents that are part of
a high quality idea are likely to have a higher expected value, and thus their location
may be more sensitive to tax. We also allow the idea level tax parameter to include a
random term ηi. This captures all components of ideas that determine the responsiveness of
location choice to tax and are observed by the parent firm but not by the econometrician.
For instance, the quality variable is likely to be an imperfect measure of the expected
value of the idea. There could be other factors that are correlated with the idea's
expected values, unobserved by us, but available to firms, which will be captured by ηi.
Similarly, we model the parameter on real innovative activity, βi, as an idea level random
coefficient; the impact of real innovative activity on the payoff function varies across
patents with the random term νi. Firms may value locating the legal ownership of
intellectual property in the same country as it was created, and the strength of this
motive is likely to vary across ideas. A central assumption of the standard multinomial
logit model is that the stochastic error term associated with the payoff from a particular
option (in our case the decision to locate ownership of a patent in a particular location)
has an iid type I extreme value distribution. This rules out correlation in latent
payoffs. This assumption leads to a closed form solution for the location choice
probabilities, which is empirically convenient. However, it is restrictive, leading the
multinomial logit model to imply restrictive substitution patterns. In particular, the
lack of correlation in payoffs endows the model with the independence of irrelevant
alternatives (IIA) property. We include in xjt a number of time varying location
characteristics that firms are likely to value when choosing where to locate the legal
ownership of intellectual property. However, there are likely to be other location
characteristics that firms value that we do not observe. To capture these we include
location–industry–firm size fixed effects, ξrj. These will control for location specific
costs, such as the legal costs associated with setting up a subsidiary, or location
specific benefits, such as government provided public goods, the relevance of which might
differ for firms of different size or industry. Note that there may be many other patent,
idea or firm specific factors that do not vary across location but that do influence the
costs or benefits of a location. However, because these do not vary across location they
will not enter the location choice decision, and therefore are not explicitly entered into
Eq. (1); including them would lead to an observationally equivalent choice model, because
they would drop out when payoff comparisons are made across locations.

<hs>  Identification</hs>
  ~~~~~~~~~~~~~~

Our primary interest lies in pinning down the ceteris paribus impact of a change in the
corporate tax rate set by any one country on the shares of patent applications made by
subsidiaries in both that and in alternative locations. To do this we must consistently
estimate the parameters of the payoff function outlined in Eqs. (1)–(4), and in particular
the parameters governing the marginal impact of tax on the payoff associated with
selecting a location, which are modelled as random coefficients. Train (2003) shows that
the random coefficient model has a duel interpretation as an error component model. Under
this representation, the mean of the random coefficient can be interpreted as a fixed
coefficient — it is pinned down by variation in location choices in response to variation
in taxes faced by firms, conditional on other observables included in the model. The
standard deviation of the random coefficient is interpreted as a component in the error
term — it is pinned down by correlation in payoffs across locations (both in a given
choice set and across location decisions within a given idea). Berry and Haile (2010) have
established that in random utility multinomial logit models the distribution of unobserved
preference parameters is non-parametrically identified given sufficiently rich micro data.
However, non-parametric estimation of this model is computationally burdensome, and we
therefore follow most papers in the literature by assuming payoffs are linear with
independent additive shocks and that the distribution of unobserved parameters is normally
distributed. These assumptions give us a convenient approximation. The standard
identification concerns still apply here; to consistently estimate the parameters we
require that the additive shock (ϵpjt) and the idea specific random terms (ηi and νi) are
independent from each other and from the other explanatory variables. Specifically, if
there are factors which influence location choice, and that are not captured by the
observed and unobserved controls that we include, this would lead to inconsistent
estimates. To mitigate this concern, we include a number of controls in the model. We
include location–industry–firm size fixed effects; these control for all country
characteristics that affect a firm's payoff and that do not vary through time, but that
potentially do vary across firms in different industries and different parent firm sizes.
We include time varying (non-tax) location characteristics. These include a measure of the
presence of real innovative activity associated with the intellectual property. This
controls for the fact that some firms, for reasons other than the tax rate they will face
in a particular location, may wish to co-locate legal ownership of intellectual property
with real innovative activity. If decisions over the location of real innovative activity
are influenced by corporate tax rates, then failure to control for this would result in an
inconsistent estimate of the impact of tax on patent location choice. We also control for
the strength of intellectual property rights protection in the location, market size and
technological innovativeness — all factors that vary over time and location, and may be
expected to impact on intellectual property location choices. Identification of the tax
coefficients also relies on the presence of informative variation in taxes in the data;
specifically we need to observe variation in the set of taxes in potential locations
across patent choice situations, conditional on all other factors that influence location
choice. Crucially, it is necessary that there is variation in differences in taxes between
locations across choice sets. So, for instance, if the only source of tax variation was
that all tax rates changed simultaneously by the same amount, the marginal effect of tax
on the payoffs would not be identified. Such variation arises in our framework for two
reasons. First, there is variation over time in statutory tax rates; as outlined below in
Section 2, over the period for which we have data (1985–2005) there has been a general
pattern of declining statutory tax rates. The size of this decline has varied across
countries, and the changes have occurred at different times, meaning that tax reforms have
given rise to variation in the set of tax rates across locations. Second, in addition to
this time series variation, CFC regimes lead to another source of variation; two parent
firms taking a decision at the same point in time, but resident in different countries,
can face a different set of tax rates due to cross country differences in CFC rules. The
variation in location choices, conditional on other factors, in response to this variation
in tax rates pins down the impact of tax on location choice.

<h>DATA</h>
----

To estimate the model we need information on where firms have chosen to locate the legal
ownership of their patents, the corporate tax regime and other conditioning variables.

<hs>  Patents data</hs>
  ~~~~~~~~~~~~

We use data on patent applications filed at the European Patent Office (EPO) by the
European and US subsidiaries of parent firms located in fourteen European countries. We
exclude from our analysis firms that patent infrequently. The number of patent
applications by location of the subsidiary that filed the patent application is shown in
Table 3.1. Our data include 1083 parent firms that collectively have 4,823 patenting
subsidiaries, which file 379,849 patent applications over the period 1985–2005. These
account for a 70% of all corporate applications filed at the EPO by firms parented in
these fourteen European countries during this period. Each patent application lists the
firm that files the application (the applicant), this is the legal owner of the patent.4
We identify the parent firm using information from company accounts (from Amadeus),
company websites, business directories and other sources (see Abramovsky et al. (2008) for
details). We use ownership information at a fixed point in time (2004), and we do not
observe changes in ownership after an application has been filed. For each patent
application this gives us a mapping between the location of the parent firm and the
location of the subsidiary that legally owns the patent. We also observe the location of
the inventors (individuals) that created the technology underlying the patent
application.5 There are often inventors located in multiple countries, and often in
different countries to that of the applicant.6 The location of both the applicant and the
inventors are distinct from the patent office to which the firm is applying for
protection. For patent applications filed at the EPO, each application also designates the
individual countries in which final patent protection will be sought; it is these
individual countries, not the EPO, that grants patent protection. We use Thomson's Derwent
database to classify patent applications based on the technology embodied in the patent
and the markets in which the technology is used. We use three broad industry groups —
Chemical, Electrical and Engineering. A patent application can be relevant for more than
one industry group if it has applicability in more than one of these industries. Where
this is the case we include the patent application in each of the industry sub-samples,
and when we calculate the market level elasticities we weight each patent application so
that the sum of the weights equals one (so if a patent application is in two industries it
will get a weight of 0.5 in each). Table 3.1 columns (2)–(4) shows the industry split of
patent applications, 32.3% are in Chemical, 36.8% in Electrical and 30.8% in Engineering,
but this varies across countries. We restrict our analysis to firms that are above the
20th percentile in terms of the number of patent applications per firm in their industry.
We distinguish large firms as those with a level of patenting above the 80th percentile in
their industry. 78.8% of patent applications in our sample are held by large firms. Firms
often take out a number of related patent applications at the same time; we allow for
correlation in these decisions. We group together related patent applications that can be
considered to be part of the same idea. We identify patent applications as part of the
same idea if they are made by the same parent firm, are filed in the same quarter (i.e.
three month period), are classified in the same industry and share a network of common
inventors. The number of patent applications in an idea varies: on average an idea
contains one patent application; ideas containing more than one application account for
26% of all patent applications. The importance of ideas in our empirical strategy is that
we allow correlation across patent applications at the level of the idea; the decisions
over where to locate ownership of these related patent applications is unlikely to be
independent, and the inclusion of random coefficients at this level allows for them to be
correlated.

     <hss>Patent quality</hss>

        There is a large literature that highlights the skewness of patent value and
        quality (Pakes (1985, 1986), Blundell et al. (1999), Lanjouw and Schankerman
        (2004) and Hall et al. (2007)). Firms file patent applications for a variety of
        reasons; some are filed to protect valuable new ideas, others are filed
        strategically to provide option values or to block competitors. Patent value also
        varies because some ideas are commercially more valuable than others. We identify
        high quality patent applications as those that are part of a triadic patent
        family, i.e. a related patent application has been filed at each of the EPO, the
        US Patent and Trademark office and the Japan Patent Office. The OECD uses triadic
        patent families “… to improve the international comparability and quality of
        patent-based indicators … patents included in the triadic family are typically of
        higher economic value: patentees only take on the additional costs and delays of
        extending the protection of their invention to other countries if they deem it
        worthwhile.” (OECD, 2012). We expect triadic patent applications to be of a higher
        value since there is a cost to filing patent applications at each of these patent
        offices, and the main incentive to do this is if firms expect the technology to
        have a wide application. Each idea (group of patent applications) is classified as
        high quality if over half of the associated patent applications are triadic. As
        seen in Table 3.1 (column (7)) on average 36.5% of patent applications are
        classified as being part of a high quality idea.

     <hss>Patent ownership and income from patents</hss>

        We model the impact of tax on where firms choose to locate the legal ownership of
        patents. In the introduction we discuss the reasons that we might expect tax to
        affect a firm's decision of where to hold legal ownership of intellectual
        property. The extent to which firms have arranged their activities in such a way
        that income can reasonably be deemed to be attributable to the subsidiary that
        legally owns the intellectual property will differ; firms will differ in how
        aggressively they seek to manage their tax liabilities. For some firms, the choice
        of where to earn income may be a choice between those countries in which real
        innovative activities already takes place; others may employ strategies that allow
        them to earn income in a separate country. There are many factors that affect the
        costs and benefits of choosing a particular location. For tax havens these costs
        may be particularly high: CFC rules are more likely to bind; the transfer of
        profits to locations where there is little real activity will be more difficult;
        tax havens are likely to be less attractive locations along non-tax dimensions
        such as intellectual property rights protection. We would not expect legal
        ownership of all patents to be located in such countries. However, it is possible
        that some firms are particularly aggressive in their tax planning and organise
        their activities in such a way that income is earned in a location that is not
        where legal ownership is located. We do not observe income flows, so we do not
        explicitly model this behaviour; to the extent that it makes the decision over the
        location of legal ownership less related to tax we would be less likely to find an
        impact of tax. In our model we aim to capture this variation in behaviour across
        firms, and within firms across ideas, by the inclusion of observed and unobserved
        heterogeneity. An additional complicating factor is that a firm might file a
        patent application from one subsidiary, but later transfer ownership of that
        patent to another related firm. However, firms have an incentive to consider tax
        when making the initial location decision, because in many situations there are
        tax costs to transferring the ownership of intangible assets. For there to be a
        tax benefit to the sale or transfer of an asset it must be the case that this can
        happen at a value below the true market value. The transfer of intellectual
        property will be subject to transfer pricing rules, which will act to limit how
        much value can be shifted to a low tax country. In addition, many European
        countries operate exit taxes that attempt to levy tax on the net present value of
        the expected revenue stream on an intangible asset when it is moved out of the
        country. Such tax provisions reduce (if not remove) any tax advantages to re-
        locating to a lower tax jurisdiction. If firms do intend, with some positive
        probability, to re-locate the ownership of a patent in the future, and if transfer
        pricing rules and exit taxes do not act to perfectly off-set any tax advantages of
        doing so, this would reduce the importance of corporate tax in the initial
        location decision. This is an additional reason that it is important that we allow
        heterogeneity in the importance of corporate tax across intellectual property. The
        place where we need to make more restrictive assumptions about the relationship
        between legal ownership and income from intellectual property is when we carry out
        the ex ante analysis of the Patent Box tax reforms and calculate the revenue
        implications of these reforms. In order to do this we need to assume that the
        relationship between legal ownership and income is not changed by the policy
        reform.

<hs>  Taxes</hs>
  ~~~~~

We measure the impact of tax on payoffs using the statutory tax rate. We assume that
returns from intellectual property are expected to be sufficiently high that deductions
such as capital allowances are relatively unimportant, so that the effective tax rate
faced by the firm is approximately the statutory tax rate (see Devereux and Griffith
(2003), where Fig. 1 shows that the marginal effective tax rate asymptotes to the
statutory tax rate as profitability increases). Our identification strategy relies on
variation over time and across countries in the tax rate. Table 3.1 (columns (8)–(11))
summarise the variation in corporate tax rates. In general, main statutory tax rates fell
in the two decades up to 2005, but with the timings of changes differing across countries.
The Scandinavian countries – Denmark, Finland, Norway and Sweden – reduced tax rates
significantly around 1990. Italy enacted a reduction of over 10 percentage points in 1998,
as did Germany in 2001. France and the UK have enacted a series of gradual reductions.
There can be additional tax levied in the parent firm's home country as a result of
Controlled Foreign Company (CFC) rules, which aim to prevent firms locating income in
lower tax countries in order to avoid taxation in their home country. CFC rules set out
criteria for identifying subsidiaries that are located in a country deemed to be ‘low-tax’
and earning a significant amount of ‘passive income’ (income that is not associated with
real activity). When a CFC regime is in place in a parent firm's country of residence, and
a subsidiary is located in a country that is deemed a ‘low tax’ location (as judged
against parent firm country specific thresholds), then we set the tax variable, τfjt,
equal to the parent firm country's statutory rate. A description of the country pairs for
which this is the case is given in Table 3.2. There is variation in whether a parent firm
country operates a CFC regime (some regimes are introduced during the period for which we
have data) and in the applicant countries that are deemed low tax (which differ over time
when statutory rates change). This definition of whether CFC rules bind effectively
assumes that the income received from a patent is deemed to be passive income, and that
the share of passive income is sufficient to trigger the CFC rules. This is clearly an
approximation. However, if we look across all location options that firms in our data face
and that are deemed low tax by CFC regimes, then it is rarely the case that the parent
firm has both inventors and holds legal ownership of a patent application in the same
location. The results we present below are robust to the alternative assumption that
patent applications with ownership located in countries where associated real innovative
activity is also located would be treated as active income, so that CFC rules do not bind.

<hs>  Descriptive statistics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

The variables included in the model are defined and summarised in Table 3.3. The top panel
contains the observed location attributes we include. These comprise the tax rate that the
parent firm would face if it earned income from the application of intellectual property
in the location, a measure of the presence of real innovative activity in a location
defined as an indicator of whether at least one of the inventors associated with the
patent applications that form the idea are located in that country and country-time
varying observable characteristics. The latter includes a measure of intellectual property
rights protection. This is based on a measure developed by Ginarte and Park (1997) and
Park (2008). The countries we consider all have advanced systems of property rights and
therefore rank relatively highly on the protection of intellectual property. We define a
country as having a strong intellectual property regime if it scores above the median of
countries in our sample. Other country-time varying variables include market size, as
measured by Gross Domestic Product (GDP) and the technological innovativeness of a
country, proxied by business R&D investment in the country as a share of GDP. We allow the
valuations firms place on location characteristics to vary across patent applications. A
summary of observable patent (or idea) characteristics is given in the bottom panel of
Table 3.3. In estimation we allow all coefficients to vary with the industry the patent
application belongs to and the size of the associated parent firm. This allows the model
to capture, for example, that large firms are more likely to have organisational
structures that assist the location of intellectual property for tax purposes. The tax
rate is interacted with a measure of the idea quality, reflecting the possibility that
firms' location choices may be more responsive to tax when they expect intellectual
property to earn higher returns.

<h>RESULTS</h>
-------

Table 4.1 shows the estimated coefficients of the choice model outlined in Section 2. The
model is estimated using simulated maximum likelihood (see Train (2003)). We allow all
coefficients to vary across industry and firms size, indicated by the different columns.
We include a full set of location–industry–firm size fixed effects (not reported in Table
4.1, but available upon request). The top row of Table 4.1 shows that the mean marginal
impact of tax on the payoff from placing legal ownership of a patent in a location is
negative and statistically significant across all industries and parent firm size groups.
The second row shows that in both the electrical and engineering industries the payoff for
high quality patents is more sensitive to taxes. This is true both for large and medium
firms. In the chemical industry the payoff for a high quality patent is estimated to be
marginally less responsive to tax than for lower quality patents for large firms, with
there being no statistically significant difference between the high and low quality
patents for medium firms. Row three shows that there is a substantial degree of unobserved
heterogeneity in the importance of tax on location choice across ideas, the standard
deviations of the random coefficients on tax are both large and statistically significant
across all industries and size categories. The fourth row shows that, ceteris paribus,
having real innovative activity in a location is associated with a higher payoff from
placing legal ownership of a patent in that location across all industries and size
categories; the fifth row shows that there is a significant amount of variation in the
importance of this characteristic across ideas. Together the large and statistically
significant standard deviations on the random coefficients on tax and real innovative
activity (in all industry-firm size groups) indicates the presence of important
correlations in payoffs, both across locations for a given patent, and across patents in a
given idea. These correlations will generate patterns of substitution that will depart
from the more restrictive patterns implied by a standard multinomial logit model. The
remaining three rows of Table 4.1 describe the impact of having strong intellectual
property protection, and the marginal impacts of market size and technological
innovativeness, on the payoff function. For five of the six industry-firm size groups, a
location having strong intellectual property protection is, all else equal, associated
with firms obtaining higher payoffs from locating legal ownership of their patents there
(the exception is medium electric firms, for which the strong intellectual property rights
dummy is negative). Larger market size is associated with statistically significantly
larger payoffs for five of the size industry-firm size groups, and a higher degree of
technological innovativeness is associated with statistically significantly larger payoffs
for four of the size industry-firm size groups. Table 4.2 shows the matrix of own and
cross tax elasticities implied by the choice model. It contains the elasticities of the
share of patents located in each of 14 European countries with respect to the rate of
corporate tax set in each of these countries and in the US. These are calculated as
described in Section 2. We report the matrix of elasticities using tax rates and the
distribution of patent applications for the most recent year in our data, 2005. Each cell
shows the elasticity of the share of patents located in the country indicated in column 1
with respect to the tax rate set by the country in row 1. The emboldened diagonal shows
the own tax elasticities. For all locations, except Luxembourg, the own tax elasticities
are less than one in magnitude. There is a limited literature on the elasticity of the
location of corporate income with respect to tax. De Mooij and Ederveen (2008) report that
empirical studies considering the effect of differences in statutory tax rates on various
measures of profitability (with a view to indirectly capturing the effects on profit
shifting) tend to find a semi-elasticity of around − 1.2. As in this paper, Karkinsky and
Riedel (2012) consider the link between corporate tax rates and patent applications. They
estimate a semi-elasticity that, depending on the functional form of their model, implies
that a 1 percentage point increase in the rate of corporate tax translates into a
3.5%–3.8% fall in patent applications from that location. Direct comparison with our
results is made difficult by the fact that our model allows tax effects to vary across all
locations. We find that the share of patents held in Luxembourg is most sensitive to tax
(the Luxembourg semi-elasticity is 3.9%) and least sensitive for Germany (the German semi-
elasticity is 0.5%).7 Theoretically, we might expect smaller countries to have relatively
high own tax elasticities, as a change in their tax rate will not affect the market rate
of return, making the cost of capital more responsive to tax changes (see Wilson (1999)).
This may be one of the reasons that such countries are more likely to compete for
corporate income using low rates; a change in the rate leads to a larger change in the
relatively small tax base (see, for example, Bucovetsky and Haufler (2007)). The own tax
elasticities in Table 4.2 show some evidence of this; they are higher for the Benelux
countries than for France and Germany. The importance of allowing for observed
heterogeneity and correlation in locations' payoffs can be seen by looking at the cross
tax elasticities. In a multinomial logit with no observed or unobserved heterogeneity all
cross tax elasticities in a column would be the same — a reduction in the tax rate in
location A would lead to patent applications switching from other locations in proportion
to their original shares. This implausibly restrictive pattern of substitution is not
imposed in our more flexible model, meaning that elasticities vary substantially within a
column. In particular, our model allows the data to capture the fact that firms are more
likely to choose to switch between locations with similar characteristics (whether that be
because the firm has inventors located in several locations, or because locations have
similar tax rates).

<h>POLICY SIMULATIONS</h>
------------------

One of the advantages of estimating the model outlined above is that it captures patterns
of substitution across locations, and it therefore allows us to simulate counterfactual
policy situations. We illustrate this by considering a recent set of policy reforms. A
number of European countries have introduced polices that offer substantially reduced
rates of corporation tax on the income derived from patents, and in some cases other forms
of intellectual property (these are often called Patent Boxes). Firms are able to declare
that some portion of their profits are derived from either the use or licence of patents,
and these profits are taxed at a lower rate. Patent Box rules differ across countries, for
example, in terms of how eligible income is measured, how the rules that apply when
calculating how much income can be allocated to patents, and how the related expenses are
treated.8 None of the countries require that the R&D underlying the intellectual property
took place in that country, as this is not permissible under European law. We use the most
recent year of our data (2005) to simulate the impact of the two sets of policies. First
we consider the introduction of Patent Boxes in the Benelux countries, and second the
later introduction in the UK. We simulate the impact of these policies on the share of new
patents for which legal ownership is placed in each of these countries using the choice
model presented above. For illustrative purposes, we assume that the total level of
patenting activity by European firms is not affected by the policy reforms. We also
consider the impact of these policy reforms on tax revenue; this requires the further
assumption that the relationship between where tax is levied and the location of legal
ownership is not altered by the policy reform. The policies are summarised in Table 5.1.
In 2007 Belgium introduced a Patent Box that reduced the tax rate on income derived from
patents from 34% to 6.8%, and the Netherlands introduced a Patent Box that reduced the
rate from 31.5% to 10%. In 2008 Luxembourg reduced the rate from 30.4% to 5.9%. The UK
government introduced a Patent Box at the rate of 10% in 2013; the main rate of corporate
tax in the UK was 30% in 2005, but had fallen to 24% by 2013. We simulate the impact of
the reduction from 30% to the Patent Box rate.9 Table 5.2 sets out the results of these
simulations for the four locations that introduced Patent Boxes.10 A note of caution in
interpreting these results is that the lowest tax rate we observe in the data is 10% in
Ireland, whereas two of the Patent Box rates are below this level, and so are outside the
observed range of taxes in our data. We carry out the simulation on the full set of patent
applications, shown in the top panel. It may be the case that many patents do not earn
much income, and so in the bottom panel we carry out the simulation using only the high
quality patents, under the assumption that these are the patents that are expected to earn
the highest income. The estimates suggest that the location of these patents were on
average more sensitive to tax. The first column shows the actual share of patent
applications in each location in 2005 (prior to the introduction of Patent Boxes). The
second column shows the predicted share of patent applications in each location after the
introduction of Benelux Patent Boxes. The standard error of these predicted shares are
shown in parenthesis. The third column expresses the % change from column 1 to column 2.
The introduction of Patent Boxes in the Benelux countries leads to a large and
statistically significant increase in the share of new patents whose legal ownership is
located in Belgium and Netherlands. The increase in Luxembourg is proportionally large,
but is not statistically significant. There is no change in the share in the UK. There is
a decline in the share of patent applications located in other non-Patent Box locations
(not shown). The fourth column shows the predicted shares after the introduction of the UK
Patent Box (in addition to the Benelux Patent Boxes). The fifth column shows the % changes
from column 1 to column 4. The UK Patent Box leads to a reduction in the share of new
patent applications made by subsidiaries located in the Benelux countries, but for Belgium
and the Netherlands they still have a statistically significantly higher share than prior
to the introduction of any Patent Boxes. The share of new patent applications made by
subsidiaries located in the UK increases by a statistically and economically significant
amount. The results with high quality patents are similar. In columns (6)–(8) of Table 5.2
we consider the impact on tax revenue from income derived from patents. These combine two
effects. The reduction in the statutory tax rate will reduce revenue, but the increase in
the share of income from patents will increase it. We demonstrate the impact on tax
revenue by computing the product of the statutory tax rate in each country and the share
of patent applications. We index this to 100 before the introduction of any Patent Boxes.
In the upper panel of the table we assume that all patents are equally valuable, and that
the relationship between legal ownership and taxable income is not affected by the reform.
All countries experience a decline in revenue. Although the countries that introduce
Patent Boxes attract more new patents, the increased share is not sufficient to outweigh
the effect of the lower tax rate. With all four Patent Box policies in place, revenues are
less than half of their previous levels in these countries. Ernst et al. (2013) provide
evidence that lower rates of tax on patent income attract particularly innovative projects
with high earning potential. In the lower panel we consider the effect on revenue when we
consider only high quality patents. The picture is here is similar; the introduction of
Patent Boxes results in a substantial reduction in revenues.

<h>SUMMARY AND CONCLUSION</h>
----------------------

The literature has emphasised the downward pressure on corporate income tax rates that
arises from factor mobility. There is also a large literature that discusses the
strategies firms use to shift income for tax purposes and to circumvent anti-avoidance
rules, and that highlights an important role for intangible assets. However, we know
relatively little about the extent to which the location of intangible assets responds to
tax. The evidence there is on the impact of tax on the location of capital more generally
has tended to suffer from the imposition of restrictive a priori assumptions placed on the
underlying model of firm behaviour. From a policy perspective it is clearly important to
understand how responsive firms are to corporate income taxes when they make location
decisions. In this paper, we estimate a model of firms' decisions over where to locate the
legal ownership of their patents. We find that corporate tax rates are an important
determinant of location choice. We extend the current literature on the determinants of
firm location choice by estimating a flexible choice model, which accounts for both
observed and unobserved heterogeneity in behaviour. We are able to generate own and cross
tax elasticities across locations that capture complex patterns of substitution in the
data. The model can be used to conduct ex ante analysis of policy changes. We find that
this heterogeneity is important for explaining location choices. Our model also shows that
other factors influence where firms choose to hold legal ownership of patents. For
instance, firms are more likely to locate patent ownership in countries where they have
associated real innovative activity. This may reflect co-location externalities, or the
influence of tax rules which seek to limit the extent to which income and real innovative
activity can be geographically separated. Firms also value other non-tax location
characteristics. Such factors, along with tax rules like the operation of CFC regimes that
limit the tax advantages of locating patent ownership in low tax jurisdictions, help
explain why we do not see firms choosing to hold all legal ownership of patents in the
lowest tax locations. We use the model to consider the impact of the recent introduction
of preferential tax regimes for income from patents. These Patent Boxes are likely to
attract patent income, but our estimates suggest that they will also lead to substantial
falls in tax revenues. Of course some of this revenue loss might be offset by gains from
attracting activities that yielded positive externalities; these would need to be taken
into account in a calculation of the welfare impact of the policy. It is also possible
that the tax reforms will affect firms' decisions over whether to apply for a patent on a
new technology or whether to rely on secrecy. We do not have information that would allow
us to directly estimate this margin, but this would be an interesting avenue for future
research. The introduction of Patent Boxes by several European countries in a relatively
short space of time has given rise to concerns that countries are engaging in tax
competition for patent income. In future work we intend to build on the framework
developed here to consider whether governments are engaged in a strategic game to attract
income from intellectual policy that ultimately will continue to exert downward pressure
on corporate taxes.


<h>REFERENCES</h>
----------

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<ART>Policing cannabis and drug related hospital admissions: Evidence from administrative records
================================================================================

Authors: Elaine Kelly, Imran Rasul
DOI: 10.1016/j.jpubeco.2014.01.008
Year: 2014  |  Pages: 89-114
ASJC codes: 2002, 2003
Keywords: Alcohol, Cannabis, Class-A drugs, Depenalization, Hospital admissions

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We evaluate the impact of a policing experiment that depenalized the possession of small quantities of cannabis in the London borough of Lambeth, on hospital admissions related to illicit drug use. To do so, we exploit administrative records on individual hospital admissions classified by ICD-10 diagnosis codes. These records allow the construction of a quarterly panel data set for London boroughs running from 1997 to 2009 to estimate the short and long run impacts of the depenalization policy unilaterally introduced in Lambeth between 2001 and 2002. We find that the depenalization of cannabis had significant longer term impacts on hospital admissions related to the use of hard drugs, raising hospital admission rates for men by between 40 and 100% of their pre-policy baseline levels. The impacts are concentrated among men in younger age cohorts. The dynamic impacts across cohorts vary in profile with some cohorts experiencing hospitalization rates remaining above pre-intervention levels three to four years after the depenalization policy is introduced. We combine these estimated impacts on hospitalization rates with estimates on how the policy impacted the severity of hospital admissions to provide a lower bound estimate of the public health cost of the depenalization policy. © 2014.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Illicit drug use generates substantial economic costs including those related to crime,
ill-health, and diminished labor productivity. In 2002, the Office for National Drug
Control Policy estimated that illicit drugs cost the US economy $181 billion (ONDCS,
2004). For the UK, Gordon et al. (2006) estimated the cost of drug-related crime and
health service use to be £15.4 billion in 2003/4. It is these social costs, coupled with
the risks posed to drug users themselves, that have led governments throughout the world
to try and regulate illicit drug markets. All such policies aim to curb both drug use and
its negative consequences, but there is ongoing debate among policy-makers as to relative
weight that should be given to policies related to prevention, enforcement, and treatment
(Grossman et al., 2002). The current trend in policy circles is to suggest regimes built
solely around strong enforcement and punitive punishment might be both costly and
ineffective. For example, after forty-years of the US ‘war on drugs’, the Obama
administration has adopted a strategy that focuses more on prevention and treatment, and
less on incarceration (ONDCS, 2011), although the two primary enforcement and policy
agencies of the Drug Enforcement Agency and the Office for National Drug Control Policy
remain more focused on traditional supply-side approaches. Other countries such as the
Netherlands, Australia and Portugal, have long adopted more liberal approaches that have
depenalized or decriminalized the possession of some illicit drugs, most commonly
cannabis, with many countries in Latin America currently debating similar moves.1 While
such policies might well help free up resources from the criminal justice system and stop
large numbers of individuals being criminalized (Adda et al., 2013), these more
liberalized policies also carry their own risks. If such policies signal the health and
legal risks from consumption have been reduced, then this should reduce prices (Becker and
Murphy, 1988). This can potentially increase the number of users as well as increasing use
among existing users, all of which could have deleterious consequences for user's health.
The use of certain drugs might also provide a causal ‘gateway’ to more harmful and
addictive substances (van Ours, 2003; Melberg et al., 2010). This paper considers the
impact of a localized policing experiment that reduced the enforcement of punishments
against the use of one illicit drug-cannabis-on a major cost associated with the
consumption of illegal drugs: the use of health services by consumers of illicit drugs.
The policing experiment we study took place unilaterally in the London Borough of Lambeth
and ran from July 2001 to July 2002, during which time all other London boroughs had no
change in policing policy towards cannabis or any other illicit drug. The experiment-known
as the Lambeth Cannabis Warning Scheme (LCWS)-meant that the possession of small
quantities of cannabis was temporarily depenalized, so that this was no longer a
prosecutable offense.2 We evaluate the short and long run consequences of this policy on
healthcare usage as measured by detailed and comprehensive administrative records on drug-
related admissions to all London hospitals. Such hospital admissions represent 60% of
drug-related healthcare costs (Gordon et al., 2006). To do so we use a difference-in-
difference research design that compares pre- and post-policy changes in hospitalization
rates between Lambeth and other London boroughs. Our analysis aims to shed light on the
broad question of whether policing strategies towards the market for cannabis impact upon
public health, through changes in the use of illicit drugs and subsequent health of drug
users. Our primary data comes from a novel source that has not been much used by
economists: the Inpatient Hospital Episode Statistics (HES). These administrative records
document every admission to a public hospital in England, with detailed ICD-10 codes for
classifying the primary and secondary causes of each individual hospital admission.3 This
is the most comprehensive health related data available for England, in which it is
possible to track the admissions history of the same individual over time. We aggregate
the individual HES records to construct a panel data set of hospital admissions rates by
London borough and quarter. We do so for various cohorts defined along the lines of
gender, age at the time of the implementation of the depenalization policy, and previous
hospital admission history. As such these administrative records allow us to provide
detailed evidence on the aggregate impact of the depenalization policy on hospitalization
rates, and to provide novel evidence on how these health impacts vary across cohorts. To
reiterate, these administrative records cover the most serious health events. Patients
with less serious conditions receive treatment elsewhere, including outpatient
appointments, accident and emergency departments, or primary care services. If such health
events are also impacted by drug policing strategies, our estimates based solely on
inpatient records provide a strict lower bound impact of the depenalization of cannabis on
public health. The balanced panel data we construct covers all 32 London boroughs between
April 1997 and December 2009. This data series starts four years before the initiation of
the depenalization policy in the borough of Lambeth, allowing us to estimate policy
impacts accounting for underlying trends in hospital admissions. The series runs to seven
years after the policy ended, allowing us to assess the long term impacts of a short-lived
formal change in policing strategy related to cannabis. Given the detailed ICD-10 codes
available for each admission, the administrative records allow us to specifically measure
admission rates for drug-related hospitalizations for each type of illicit drug: although
the depenalization policy would most likely impact cannabis consumption more directly than
other illicit drugs, this has to be weighed against the fact that hospitalizations related
to cannabis usage are extremely rare and so policy impacts are statistically difficult to
measure along this margin. Our main outcome variable therefore focuses on hospital
admissions related to hard drugs, known as ‘Class-A’ drugs in England. This includes all
hospital admissions where the principal diagnosis relates to cocaine, crack, crystal-meth,
heroin, LSD, MDMA or methadone.4 The administrative records also contain information on
the length of hospital stays (in days) associated with each patient admission, and we use
this to explore whether the depenalization policy impacted the severity of hospital
admissions (not just their incidence), where the primary diagnosis relates to
hospitalizations for Class-A drug use. Ultimately, we then combine the estimated policy
impacts on hospitalization rates and the severity of hospital admissions for Class-A drug
use, to provide a conservative estimate of the public health costs of the depenalization
policy that arises solely through the increased demand on hospital bed services. We
present four main results. First, relative to other London boroughs, the depenalization
policy had significant long term impacts on hospital admissions in Lambeth related to the
use of Class-A drugs, with the impacts being concentrated among men. Exploring the
heterogeneous impacts across male cohorts, we find the direct impacts on Lambeth residents
to be larger among cohorts that were younger at the start of the policy. The magnitudes of
the impacts are large: the increases in hospitalization rates correspond to rises of
between 40 and 100% of their pre-policy baseline levels in Lambeth, for those aged 15–24
and aged 25–34 on the eve of the policy. To underpin the credibility of the difference-in-
difference research design, we also probe the data to: (i) check for pre-existing
divergent trends in hospitalization rates between Lambeth and other London boroughs; (ii)
evaluate the robustness of the results to alternative control boroughs to compare Lambeth
to; (iii) examine whether differential changes over time in health care provision between
Lambeth and other locations, or other policies impacting hospitalizations for Class-A drug
use, could confound the results, and; (iv) shed light on whether individuals changed
borough of residence in response to the policy. Second, the dynamic impacts across cohorts
vary in profile with some cohorts experiencing hospitalization rates remaining above pre-
intervention levels three to four years after the depenalization of cannabis was first
introduced. Third, we explore the impacts of the policy on hospitalizations related to
alcohol use among Lambeth residents. There is a body of work examining the relationship
between cannabis and alcohol use: this has generated mixed results with some research
finding evidence of the two being complements (Pacula, 1998; Williams et al., 2004), and
other studies suggesting that the two are substitutes (DiNardo and Lemieux, 2001; Crost
and Guerrero, 2012). We add to this debate using a novel policy experiment and
administrative data. Our results suggest that for the youngest age cohort, if
depenalization causes the price of cannabis to fall, then alcohol and cannabis might well
be substitutes. However for older age cohorts, we find no evidence that the policy leads
to increased admissions related to alcohol use, or the combined use of alcohol and Class-A
drugs. Finally, the severity of hospital admissions, as measured by the length of stay in
hospital, significantly increases for admissions related to Class-A drug use. We then
combine this impact with our baseline estimated impacts on hospitalization rates by age
cohort, to calculate the annual cost of the policy. We find the increased hospitalization
rates and length of stays conditional on admission to be around £80,000 per annum, and
this more than offsets the downward time trend in hospital bed-day costs that exists in
the rest of London in the post-policy period. Taken together, our four classes of results
suggest that policing strategies towards the market for cannabis have significant, nuanced
and long lasting impacts on public health. Our analysis contributes to understanding the
relationship between drug policies and public health, an area that has received relatively
little attention despite the sizable social costs involved. This partly relates to well
known difficulties in evaluating policies in illicit drug markets: multiple policies are
often simultaneously targeted towards high supply locations; even when unilateral policy
experiments or changes occur they often fail to cause abrupt or quantitatively large
demand or supply shocks, and data is rarely detailed enough to pin down interventions in
specific drug markets on other drug-related outcomes (DiNardo, 1993; Caulkins, 2000; Chu,
2012). Our analysis, that combines a focused policy and administrative records, makes some
progress on these fronts. To place our analysis into a wider context, it is useful to
compare our findings with two earlier prominent studies linking illicit drug enforcement
policies and health outcomes: Model (1993) uses data from the mid-1970s to estimate the
impact on hospital emergency room admissions of cannabis decriminalization, across 12 US
states. She finds that policy changes led to an increase in cannabis-related admissions
and a decrease in the number of mentions of other drug related emergency room admissions,
suggesting a net substitution towards cannabis. Our administrative records also allow us
to also check for such broad patterns of substitution or complementarity between illicit
drugs. Our results suggest that the depenalization of cannabis led to longer term
increases in the use of Class-A drugs, as measured by hospital inpatient admissions rather
than emergency room admissions as in Model (1993).5 More recent evidence comes from Dobkin
and Nicosia (2009), who assess the impact of an intervention that disrupted the supply of
methamphetamine in the US by targeting precursors to methamphetamine. They document how
this led to a sharp price increase and decline in quality for methamphetamine. Hospital
admissions mentioning methamphetamine fell by 50% during the intervention, while
admissions into drug treatment fell by 35%. Dobkin and Nicosia (2009) find no evidence
that users substituted away from methamphetamine towards other drugs. Finally, Dobkin and
Nicosia (2009) find that the policy of disrupting methamphetamine supply was effective
only for a relatively short period: the price of methamphetamine returned to its pre-
intervention level within four months and within 18 months hospital admissions rates had
returned to their baseline levels. In contrast, the cannabis depenalization policy we
document has an impact on hospitalization rates that, for many cohorts, lasts for up to
four years after the policy was initiated and despite the fact that the policy itself was
only formally in place for one year.6 The paper is organized as follows. Section 2
describes the LCWS and the existing evidence on its impact on crime. Section 3 details our
administrative data, discusses the plausibility of a link between policing-induced changes
in the cannabis market and the consumption of Class-A drugs, and describes our empirical
method. Section 4 presents our baseline results which estimate the impact of the LCWS by
cohort and the associated robustness checks to underpin the credibility of the research
design. Section 5 presents extended results related to dynamic effects, spillovers in
alcohol-related admissions, and the severity of admissions. Section 6 estimates the public
health costs of the policy. Section 7 discusses the broader policy implications of our
findings, and the potential for opening up a research agenda on the relationship between
police behavior and public health.

<h>THE LAMBETH CANNABIS WARNING SCHEME (LCWS)</h>
------------------------------------------

The Lambeth Cannabis Warning Scheme (LCWS) was unilaterally introduced into the London
borough of Lambeth on 4th July 2001 by the borough's police force. The scheme was
initially launched as a pilot intended to last six months, and represented a change in
policing policy towards the market for cannabis. Under the scheme, those found in
possession of small quantities of cannabis for their personal use in Lambeth: (i) had
their drugs confiscated; (ii) were given a warning rather than being arrested.7 The main
reason behind the policy change was to reduce the number of individuals being criminalized
for consuming cannabis, and to free up police time and resources to deal with more serious
crimes, including those related to hard drugs or ‘Class-A drugs’ (Dark and Fuller, 2002;
Adda et al., 2013). The underlying motivations for the policy, as well as the way in which
it was implemented and the targeted outcomes, were very similar to the way in which
cannabis depenalization policies have often been implemented throughout the world. In
keeping with other experiences of depenalization, the primary motivation behind the policy
was to free up police time and resources to tackle other crimes, and there was little or
no discussion of the depenalization policy's potential impact on public health. To this
extent our results can be informative of the existence of links between police drugs
policy and public health in settings outside of the specific London context we study.8
Anecdotal evidence suggests that local support for the scheme began to decline once the
policy was announced to have been extended beyond the initial six-month pilot. Media
reports cited that local opposition arose due to concerns that children were at risk from
the scheme, and that the depenalization policy had increased drug tourism into Lambeth.
The LCWS formally ended on 31st July 2002. Post-policy, Lambeth's cannabis policing
strategy did not return identically to what it had been pre-policy, partly because of
disagreements between the police and local politicians over the policy's true impact.
Rather, it adjusted to be a firmer version of what had occurred during the pilot so that
police officers in Lambeth continued to issue warnings but would now also have the
discretion to arrest where the offense was aggravated.9 Hence our measured long run
impacts of the depenalization policy capture the total effects arising from: (i) the long
run impact of the introduction of the depenalization policy between June 2001 and July
2002; and (ii) any permanent differences in policing towards cannabis between the pre-
policy and post-policy periods. The impact of the LCWS depenalization policy on patterns
of crime in Lambeth and other boroughs is extensively studied in Adda et al. (2013). For
the purposes of the current study on the relationship between drug-policing and public
health, three key results on the impact of the localized depenalization policy on crime
need to be borne in mind: its impact on the market for cannabis in Lambeth, its impact on
the market for Class-A drugs, and drug tourism induced into Lambeth from other parts of
London due to interlinkages in illicit drug markets across boroughs. First, Adda et al.
(2013) find that the LCWS led to a significant and permanent rise in cannabis related
criminal offenses in Lambeth. Using finely disaggregated data by type of drug offense,
they find that both the demand and supply of cannabis are likely to have risen
significantly in Lambeth after the introduction of the depenalization policy, and that
this impact persists into the long run, well after the LCWS policy officially ended. This
result is important for the current study because it suggests that the depenalization
policy caused an abrupt, quantitatively large and permanent shock to the cannabis market,
leading to the equilibrium market size to have likely increased by around 60% in the
longer term, as proxied by the number of criminal offenses for cannabis possession.10
Second, this expansion will consequently affect the equilibrium market size for Class-A
drugs if the markets are related in some way, either because of economies of scale in
supplying both drug markets, or because on the demand side preferences are such that
cannabis and Class-A drugs are complements/substitutes. Along these lines, Adda et al.
(2013) report that the longer term effect of the LCWS was to lead to a significant
increase in offenses related to the possession of Class-A drugs: offense rates for the
possession of such substances rose by 12% in Lambeth in the post-policy period relative to
the rest of London. However, there is little evidence that the police reallocated their
efforts towards crimes relating to Class-A drugs: Adda et al. (2013) report no change in
police effectiveness against Class-A drug crime in Lambeth based on two out of four such
measures (arrest and clear-up rates). Rather, Adda et al. (2013) document that the policy
appears to have allowed the police to reallocate effort towards non-drug crime. The fact
that the LCWS policy did not lead to a major reallocation of police resources towards
crime related to Class-A drugs suggests that in the current study, any link between the
depenalization policy and hospitalizations for Class-A diagnoses most likely stems from
the interlinkages between the demand sides of the markets for cannabis and Class-A drugs.
Given the addictive nature of Class-A drugs, potential lags between cannabis use and the
use of Class-A drugs later in life, and potential lags in seeking out and receiving
treatment (Fergusson and Horwood 2000; Patton et al., 2002; Arseneault et al., 2004), we
might also reasonably expect any impact of the LCWS on hospital admissions related to
Class-A drug use to last well into the post-policy period. We therefore later consider how
the effects of the LCWS on drug-related hospital admissions evolve over time. Third, Adda
et al. (2013) document how the LCWS likely induced drug tourism into Lambeth. Such changes
in the location where individuals decided to purchase cannabis stems from the fact that
local markets for illicit drugs are inherently interlinked across London boroughs. To
explore this further in terms of health outcomes, we later investigate whether there is
any evidence of individuals permanently changing their actual borough of residence to
Lambeth, after the LCWS is introduced. Standard consumer theory provides clear set of
predictions on how such depenalization policies can impact the use of cannabis and other
illicit drugs. Most existing studies assume that such policies cause significant
reductions in the price of cannabis (Thies and Register, 1993; Grossman and Chaloupka,
1998; Williams et al., 2004). This will, all else equal, increase the demand for cannabis
in part because of greater demands from existing users and also because of an impact on
the extensive margin so that new individuals choose to start consuming cannabis at the
lower price. This will have a positive impact on the consumption of Class-A drugs if
cannabis and Class-A drugs are contemporaneous complements in user preferences. It will
also increase the demand for Class-A drugs over time if the use of cannabis serves either
as a gateway to the use of other harder illicit drugs, or there is state dependence so
that cannabis users have particular characteristics that also lead them to subsequently
misuse Class-A drugs. Of course if cannabis and Class-A drugs are substitutes, then the
increased demand for cannabis resulting from the depenalization of cannabis possession
should reduce Class-A drug use and related hospitalizations. Such cross price impacts
might also exist between cannabis and alcohol (Pacula, 1998; DiNardo and Lemieux, 2001).
Hence we later also examine how hospitalization rates for diagnoses primarily related to
alcohol use respond to the depenalization policy.

<hs>  Administrative records on hospital admissions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Data on hospital admissions are drawn from the Inpatient Hospital Episode Statistics
(HES). These provide an administrative record of every inpatient health episode, defined
as a single period of care under one consultant in an English National Health Service
hospital.11 These administrative records are the most comprehensive data source on health
service usage for England. Inpatients include all those admitted to hospital with the
intention of an overnight stay, plus day case procedures when the patient is formally
admitted to a hospital bed. As such, these records cover the most serious health events.
Patients with less serious conditions receive treatment elsewhere, including outpatient
appointments, accident and emergency departments, or primary care services. If such health
events are also impacted by the depenalization policing strategy, our estimates based
solely on inpatient records provide a strict lower bound impact of the policy on public
health. For each patient-episode event in the administrative records, the data record the
date of admission, total duration in hospital, and ICD-10 diagnoses codes in order of
importance. Background patient information covers their age, gender, and their zip code of
residence at the time of admission.12 As discussed in more detail later, some specialist
services required to treat diagnoses involving the use of Class-A drugs, such as those
relating to mental health, are concentrated in a small subset of facilities that are
dispersed across London. Each of these specialist facilities would be expected to treat
patients from across London. Hence the geographic information we use to understand the
impact of the localized LCWS policy relates to the patient's borough of residence, not the
borough in which they are hospitalized. This helps ameliorate concerns that any changes in
drug related hospitalization rates are driven by changes in the provision of specific
drug-related services through specialized hospitals in London (that serve individual
residents in multiple boroughs). In Section 4.2 we provide evidence ruling out potentially
confounding changes on the supply side of medical care for heavy users of Class-A drugs.
Hence, any documented change in hospital admissions for Class-A drug related diagnoses in
Lambeth following the introduction of the LCWS might then operate through two mechanisms:
(i) a change in behavior of those residents in Lambeth prior to the policy; and (ii) a
change in the composition of Lambeth residents, with the policy potentially inducing a net
inflow of people into the borough with a higher propensity for Class-A drug use. In
Section 4.2 we use our data to examine the relative importance of these channels: we find
little evidence of systematic changes of residence in response to the policy, implying
that most of the impacts are driven by changes in behavior among those already residing in
Lambeth pre-policy. The administrative records also allow us to create panels based on
prior histories of patient admissions because the HES records have unique patient
identifiers that allow the same patient to be tracked over episodes between 1997 and 2009.
We focus on histories of admissions related to the use of either drugs (Class-A drugs,
cannabis, or other illicit drug), or alcohol, and create panels by borough-quarter-age
cohort-gender, for those with and without pre-policy histories of admissions related to
drugs or alcohol. Among those with no pre-policy admissions, we calculate admission rates
as per Eq. (1), where by construction of this admission rate is zero before the policy.
For this group, we effectively estimate whether the depenalization policy differentially
impacted hospital admission rates between Lambeth and other non-neighboring boroughs in
the period after the policy is first initiated. For those with pre-policy admission rates
(an obviously far smaller group of individuals than those without admission histories), we
change the numerator in the admission rate to reflect the relevant ‘at risk’ population:
hence Popby is replaced by the number of distinct individuals admitted for diagnoses
related to illicit drugs or alcohol while residing in borough b in the pre-policy period
between April 1997 and June 2001 (which given the small number of individuals with
histories of such hospitalizations, is not measured in thousands). The depenalization
policy likely lowers prices for cannabis in Lambeth, all else equal. Depenalization might
then impact hospitalizations for Class-A diagnoses differently across cohorts based on
their prior histories of illicit drug use. Among those with no prior history of
hospitalization for drug or alcohol use, the reduced price of cannabis induced by the
policy might lead to greater consumption of Class-A drugs if they are complements to
cannabis, or, for example, cannabis acts as a gateway to such substances. To be clear,
among these cohorts we pick up the combined impacts among those that were previously using
illicit drugs (and potentially other substances) but not so heavily so as to induce
hospitalizations, as well as those that begin to use cannabis and Class-A drugs for the
first time as a result of the reduced price of cannabis. The administrative data utilized
does not allow us to separate out the policy impacts stemming from each type of
individual. Among the cohorts with histories of hospitalization for drug or alcohol use
even before the LCWS is initiated, there are likely to be long term and heavy users of
illicit substances. Such individuals' consumption of Class-A drugs might reasonably be
more habitual and so less sensitive to changes in the price of cannabis, so that this
cohort might be less impacted by the depenalization policy, all else equal.

<hs>  Cannabis and Class-A drug use</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our primary interest is to understand how changes in police enforcement strategies towards
the cannabis market-as embodied in the LCWS policy impact public health through changes in
hospitalization rates related to illicit drug use. Of course the policy would most
directly affect the consumption of cannabis, but changes in inpatient hospital admissions
related to cannabis use are statistically hard to detect given the rarity of such events,
as documented in detail below. It is therefore instructive to first compare rates of drug
related hospital admissions from the HES administrative records, to rates of self-reported
drug use from household surveys the most reliable of which is the British Crime Survey
(BCS). Estimates from the BCS in 2002/3 indicate that cannabis was by far the most popular
illicit drug, with 16% of 16–24 year-olds and 9% of 25–34 year-olds reporting to have used
cannabis in the month prior to the survey. The corresponding figures for Class-A drug use
are just 4% and 2% respectively (Condon and Smith, 2003). The HES records show that there
are seven times as many inpatient hospital admissions for Class-A drugs than for cannabis.
This reinforces the notion that cannabis related policing policies such as the LCWS, may
not lead to a rise in statistically detectable cannabis related to hospital admissions
even if there is a substantial increase in cannabis usage caused by the policy. What is
important for our analysis is that a body of evidence suggests the cannabis and Class-A
drug markets are linked: while little is known about such potential linkages on the supply
side, on the demand side this might be because cannabis users are more likely to consume
Class-A drugs, both contemporaneously and in the future. There are of course multiple
explanations for this positive correlation between admissions for cannabis and subsequent
usage of Class-A drugs. One explanation is state dependence so that cannabis users have
particular characteristics that also lead them to subsequently misuse Class-A drugs, a
channel shown to be of first order importance using data from the NLSY97 by Deza (2011).
Alternatively, the use of cannabis might act as a causal gateway to the use of harder
drugs, has been suggested by Beenstock and Rahav (2002); van Ours (2003); Bretteville-
Jensen et al. (2008) and Melberg et al. (2010). Clearly the empirical debate on the
relative importance of state dependence and gateway impacts is far from settled. For our
study what is important is that some correlation between the market sizes for cannabis and
other illicit drugs exists, be it either because of state dependence or gateway effects.
To show the relatedness between these markets as recorded in the hospital admission
records we exploit, we present descriptive evidence from the HES to suggest how cannabis
consumption today might correlate to Class-A drug use in the future. To do so we exploit
the individual identifiers in the administrative records, allowing us to track the same
person over time. We then calculate the probability, conditional on an admission in 1997
or 1998, of being readmitted to hospital at least once between 2000 and 2004. Four groups
of admission are considered: (i) “cannabis admissions”, who were admitted for cannabis;
(ii) “Class-A admissions”, who were admitted for the use of a harder drug; (iii) “alcohol
admissions”, who were admitted for alcohol-related diagnoses; (iv) “all other admissions”,
who were admitted for any other cause and serve as a benchmark for the persistence of ill-
health over these time periods. Table 1 shows the mean and standard deviation for each
probability of readmission, conditional on prior admissions.15 Two points are of note.
First, there is substantial persistence in hospital admissions for the same risky
behavior, as shown on the leading diagonal in Columns 1–3. Persistence is particularly
high for Class-A drugs and alcohol, where 26 and 23% of individuals respectively, were
readmitted for the ill-effects of the same risky behavior over the two time periods.
Reading across the last row of Table 1 on subsequent readmission to hospital from 2000 to
2004 for any diagnosis unrelated to drugs or alcohol, we see that this readmission
probability is between 15 and 28% conditional on having been previously admitted in 1997–8
for some risky behavior related to illicit drug or alcohol use. Second, although
admissions for any form of risky behavior in 2000–4 is best predicted by admission for the
same behavior in 1997–8, we note that for those admitted for Class-A drugs in 2000–4, 5.4%
will have been admitted for cannabis related diagnoses in 1997–8. This is significantly
higher than having been previously admitted for alcohol-related diagnoses (2.2%) over the
same period. This highlights the particularly robust correlation between cannabis use at a
given moment in time, and future hospital admissions for Class-A related drug use. In this
paper our focus is on establishing whether a change in police enforcement in the cannabis
market — as embodied in the LCWS — has a causal impact on hospital admissions for Class-A
drugs. The evidence presented in Table 1 and the existing evidence documenting a linkage
between cannabis consumption on the subsequent use of other illicit substances, suggests
that as long as the policy affects the usage of cannabis consumption in some way, this is
likely to have a knockon effect on the usage of Class-A drugs in the long run. It is these
longer term effects on public health that we now focus on.

<hs>  Empirical method</hs>
  ~~~~~~~~~~~~~~~~

β0 captures London-wide cohort trends (excluding Lambeth's neighbors) in hospitalization
rates occurring at the same time as the LCWS was in operation in Lambeth. β2 captures
longer term London-wide cohort trends in hospitalization rates for the age cohort after
the depenalization policy in Lambeth officially ends. This coefficient mostly picks up the
natural time profile of any change in hospitalizations as the cohort ages say because of
varying usages of illicit substances, or changes in susceptibility to the same levels of
usage. These coefficients also partly pick up any impacts on hospitalization rates related
to diagnosis-d for London and nationwide policies, including the nationwide depenalization
of cannabis possession that occurred from January 2004 through to January 2009.16 The
parameters of interest are estimated using a standard difference-in-difference research
design: β1 and β3 capture differential changes in hospital admission rates for a given age
cohort, in Lambeth during and after the depenalization policy period, relative to other
London boroughs excluding Lambeth's neighbors. Our research design identifies whether: (i)
hospitalization rates in Lambeth significantly diverge away from London-wide cohort trends
during and after the depenalization policy is in place; and (ii) these divergences
coincide with the depenalization policy's operation in Lambeth. In Xbqy we control for two
sets of borough-specific time varying characteristics. The first contains the shares of
the population under 5 and over 75 (by borough and year), who place the heaviest burden on
health services. Second, Xbqy includes controls for admission rates, by borough-quarter-
cohort, for conditions that should be unaffected by the LCWS, in particular malignant
neoplasms, diseases of the eye and ear, diseases of the circulatory system, diseases of
the respiratory system, and diseases of the digestive system. These capture
contemporaneous changes in healthcare provision or levels of illness in the population
that could affect drug-related admissions. The admission rates for these diagnoses are all
constructed from the HES administrative records. The fixed effects capture remaining
permanent differences in admissions by borough (λb) and quarter (λq). Observations are
weighed by borough shares of the London-wide population. Defining t as quarters since
April 1997: t = [4 × (y − 1997)] + q, we assume a Prais–Winsten borough specific AR(1)
error structure, ubqy = ubt = ρbubt − 1 + ebt, where ebt is a classical error term. ubqy
is borough specific heteroskedastic, and contemporaneously correlated across boroughs.17
As with any difference-in-difference research design, the coefficients of interest measure
causal impacts only under some identifying assumptions. First, we have to assume common
trends in hospitalization rates between Lambeth and the rest of London. We later present
evidence to establish whether there is any evidence of such convergent/divergent trends in
the pre-policy period, and we also estimate our baseline specifications allowing for
borough specific linear time trends. Second, we require that there is no ‘Ashenfelter
dip’, which might otherwise indicate that the policy was introduced in response to
divergent/convergent hospitalization rates between Lambeth and the rest of London. The
descriptive time series evidence presented below helps ameliorate this concern. Third, we
require there to be no confounding changes on the supply side of medical care impacting
hospital admissions for Class-A drug use, nor any other confounding policies impacting
such outcomes. We later provide descriptive evidence to show how the availability of
health care in Lambeth for such diagnoses changed over time. We also show the impacts of
the LCWS on Class-A admissions in Lambeth prior to the introduction of the nationwide
depenalization policy in 2004. Fourth, we require that there is no differential change in
the underlying populations who are resident in Lambeth and the rest of London that might
drive divergences in hospitalization rates for Class-A admissions. Given our
hospitalization rates are based on borough of residence and not borough of treatment, we
later discuss, given the available evidence, the plausibility of individuals with
differing propensities for drug use changing their borough of residence in response to the
policy.

     <hss>Hospitalization counts</hss>

        Table 2 shows the raw count data (Totdbqy) for the average number of hospital
        admissions for diagnosis d, that occur in borough b in quarter q in year y,
        covering diagnoses related to the use of illicit substances such as Class-A drugs
        and cannabis, as well as for alcohol (in each case we show the sum of primary and
        secondary diagnoses). We break down admission numbers for Lambeth and the rest of
        London, averaging over the pre-policy and post-policy periods. Given that
        hospitalization rates for such diagnoses are higher for men than women, Table 2
        presents the data for three male age cohorts, where age is defined on the eve of
        the introduction of the LCWS policy. Three points are of note. First, admission
        rates for Class-A related diagnoses are low in absolute numbers in the pre-policy
        period for all age cohorts. These low levels of baseline counts imply that large
        percentage increases can be generated by a small change in the absolute number of
        admissions related to the use of Class-A drugs. Second, for the younger two age
        cohorts, admission numbers for Class-A diagnoses rise dramatically post-policy. In
        each case, the absolute increase between the post- and pre-policy periods is
        larger in Lambeth than the rest of London average (despite Lambeth having higher
        admission counts than other London boroughs pre-policy for all age cohorts). For
        the oldest cohort, those aged 35–44 on the eve of the LCWS policy, the count data
        suggest a slight fall in Class-A admissions in Lambeth but a rise in the average
        for the rest of London. These broad descriptive patterns in absolute counts will
        be replicated later in the formal analysis when Eq. (2) is estimated for admission
        rates. The third point of note from Table 2 on counts relates to diagnoses for
        cannabis or alcohol. We see that for each male age cohort, admission counts for
        cannabis related diagnosis are considerably rarer than for Class-A related
        diagnoses, and this remains true post-policy. As argued above, using these
        administrative records on hospital admissions, it is therefore considerably harder
        to statistically detect any significant impact of the LCWS on cannabis use through
        hospitalizations for cannabis. In contrast, we see that alcohol-related hospital
        admissions are the most frequent for all age cohorts: pre-policy, there are around
        four times as many such admissions in London on average than for Class-A related
        diagnoses. Given the body of existing evidence on potential interlinkages between
        the use of cannabis, Class-A drugs and alcohol, we later examine whether the
        depenalization policy had any impact on hospital admissions involving alcohol-
        related diagnoses.

     <hss>Unconditional impacts of hospitalization rates</hss>

        The core outcome considered in the empirical analysis is hospital admissions rates
        as defined in Eq. (1). Fig. 1A shows the time series for hospital admission rates
        in Lambeth against the rest of London averages, for each male age cohort. Each
        figure is centered on the time of policy change in Lambeth: the dashed red lines
        indicate the start and end points of the official period of operation of the LCWS
        policy. Each time series is averaged annually. In order to line up with the policy
        period, each year starts from Q3 of that year and averages to Q2 in the following
        year (so for example the value for 1997 is the average over 1997Q3–1998Q2).
        Although the time series for Lambeth is quite volatile, three points emerge from
        the comparison with other London boroughs: (i) there is no systematic difference
        in pre-trends between Lambeth and the rest of London at least for the two older
        age cohorts, nor is there any evidence of an ‘Ashenfelter dip’ in admission rates
        in Lambeth just prior to the introduction of the LCWS; (ii) there are divergences
        in admission rates in Lambeth relative to the rest of London for each age cohort;
        and (iii) London wide time series in hospital admission rates appear rather flat
        and not trending upwards or downwards, certainly for the two older age cohorts.
        Fig. 1B repeats the figures comparing Lambeth only to other boroughs with a
        similarly (high) incidence of Class-A drug related hospital admission pre-policy.
        The same broad patterns can be seen in the three time series for each male age
        cohort in Lambeth against this control group.18 Table 3 then provides descriptive
        evidence on the unconditional long term effects of the depenalization policy on
        Class-A related hospital admission rates, with each row showing hospital admission
        rates (Admitdbqy) as defined in Eq. (1). We again first focus on male cohorts of
        various ages on the eve of the LCWS policy. Columns 1 and 2 present mean hospital
        admission rates related to Class-A drug usage in Lambeth during the pre-policy and
        post-policy periods respectively; Columns 3 and 4 give the corresponding
        statistics for the average borough in the rest of London (excluding Lambeth's
        neighboring boroughs). Pre-policy, Lambeth had substantially higher rates of
        admissions than the London average. Indeed, in ranking boroughs by their per-
        policy hospital admission rates related to Class-A drugs, Lambeth has the third
        highest for men and the second highest for women. However, as suggested in Fig. 1
        and shown more formally later, there is no evidence of diverging or converging
        trends in Class-A related hospital admission rates between Lambeth and the London
        average in the pre-policy period from 1997 to 2001. In Lambeth, admission rates in
        the pre-policy period are lowest for the youngest cohort, reflecting the overall
        pattern of drug admissions by age. Comparing Columns 1 and 2 re-iterates the basic
        pattern of potential health impacts of the depenalization policy, that was
        previously shown in the raw counts data in Table 2: hospital admission rates in
        Lambeth rise over time for the 15–24 and 25–34 cohorts, but fall slightly for the
        oldest cohort. In contrast for the rest of London admission rates rise only for
        the youngest cohort and are stable or declining for the older two age cohorts.
        Columns 5 and 6 then present difference-in-difference estimates of how Class-A
        drug admission rates relate to the LCWS policy. Column 5 shows that unconditional
        on any other factor, admission rates for both the 15–24 and 25–34 cohorts
        significantly rise in Lambeth relative to the London borough average, after the
        introduction of the policy to depenalize the possession of cannabis. The relative
        increases in admission rates of .054 and .079 per thousand population for the
        youngest two age cohorts are statistically significant at the 5% level: the
        increases correspond to a 146% rise relative to the pre-policy level for the 15–24
        cohort, and a 44% increase above the baseline level for the cohort aged 25–34 on
        the eve of the policy. The effect for the oldest cohort is not statistically
        significantly different from zero. Column 6 then shows this basic pattern of
        difference-in-differences to remain in magnitude and significance once borough and
        quarter year fixed effects are controlled for. These results suggest that among
        younger male age cohorts, the policy of depenalizing the possession of cannabis is
        associated with significantly higher hospitalization rates in Lambeth for Class-A
        drug use in the longer term. Table A1 shows the corresponding results for female
        age cohorts: we find no significant impacts on Class-A related hospitalization for
        any female age cohort. The rate of admissions for such diagnoses among women is
        generally lower than among men and this might be one reason that it is harder to
        statistically detect any impact at conventional significance levels. At the same
        time, the fact that there are very different trends in hospitalizations for
        Class-A drugs across genders within Lambeth, suggests that the earlier results for
        men are not merely picking up other changes in hospital behavior or how diagnoses
        are recorded within Lambeth, that might otherwise have been expected to impact men
        and women equally. Table A2 shows the corresponding descriptive evidence for
        hospital admissions related to cannabis use for male cohorts. Cannabis hospital
        admission rates are generally lower than for Class-A drugs, especially among older
        age cohorts, despite much higher levels of cannabis usage as suggested by survey
        data. The difference-in-difference results suggest the LCWS had no significant
        impact on hospital admissions for cannabis: the point estimates for the youngest
        male cohorts are positive but not precisely estimated, and a similar set of
        findings is obtained when examining the impact of the depenalization policy on
        hospitalizations for cannabis related diagnoses among female cohorts (not shown).
        To relate these findings to the literature, recall that Model (1993) find that the
        de facto decriminalization of cannabis in twelve US states from the mid-1970s
        significantly increased cannabis-related emergency room admissions. Chu (2012)
        similarly finds that the passage of US state laws that allow individuals to use
        cannabis for medical purposes leads to a significant increase in referred
        treatments to rehabilitation centers. Our evidence from London suggests that if a
        similar effect occurs from the depenalization of cannabis possession, it does not
        then feed through to significantly higher rates of hospitalization that involve
        extreme consequences on health leading to overnight hospital stays, which is what
        our inpatient administrative data measures. For the bulk of our core analysis, we
        therefore continue to focus on Class-A drug-related hospital admissions among men.

<hs>  The impact of the LCWS by cohort</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Table 4 presents estimates of the full baseline specification (2), where we consider the
impact of the LCWS on Class-A drug related hospital admission rates for three male age
cohorts in Columns 1 to 3. These findings represent our core results: they show that the
addition of time varying borough controls (Xbqy) produces estimates very similar to the
unconditional estimates shown in Table 2. The first row shows that in the longer term
post-policy period, there are statistically significant rises in admission rates of .038
and .075 for the youngest two cohorts in Lambeth, relative to other non-neighboring London
boroughs. In line with the earlier descriptive evidence, no policy impact is found on the
oldest age cohort, who were aged 34–44 on the eve of the LCWS's introduction in Lambeth.
Comparing these increases in admission rates to the mean admission rate in Lambeth pre-
policy as reported at the foot of Table 4, the percentage increases conditional on other
factors are 103% for the youngest age cohort, and 42% for those men aged 25–34 on the eve
of the policy, which are slightly smaller than the unconditional percentages reported in
relation to Table 3. The second row of Table 4 shows that in the short-run, during the 13
months in which the LCWS was actually in operation, there are no statistically significant
effects on hospitalization rates for any cohort. Hence, as might be expected, any impact
of the cannabis depenalization policy on hospitalization rates for Class-A drug use takes
time to work through (in line with the descriptive evidence in Table 1). Table 4 also
shows the estimates of β0 and β2. These highlight that for London as a whole (excluding
Lambeth's neighbors), there are no significant long-term time cohort trends in admission
rates during and after the policy period for the older two cohorts. For the youngest
cohort aged 15–24 (column 1), hospital admission rates for Class-A drug related admissions
are naturally rising over time as the cohort ages, but the results overall show that
hospitalization rates in Lambeth are significantly diverging away from this London-wide
average in the post-policy period, all else equal. Taken together, our results suggest
that the depenalization of cannabis led to longer term increases in the use of Class-A
drugs and subsequent hospitalizations related to Class-A drug use among the two youngest
aged cohorts on the eve of the LCWS policy. If depenalization led to a decline in the
equilibrium price of cannabis in Lambeth, as is often argued to be an unambiguous effect
of such policies (Kilmer et al., 2010), then this result suggests that cannabis and
Class-A drugs have a negative cross-price elasticity, so that the two types of illicit
drug are contemporaneous complements, or the use of cannabis leads through some mechanism
to the later use of harder illicit drugs.20 This would be in line with some other studies
that have estimated the cross-price elasticity between cannabis and a specific Class-A
drug: cocaine, either using decriminalization as a proxy for a price reduction (Thies and
Register, 1993; Grossman and Chaloupka, 1998), or using actual price information (Williams
et al., 2004). An obvious concern with these results is that they might in part be
confounded by natural time trends, by age cohort, in hospitalization rates for Class-A
drugs, that are not fully being captured in the policy and post-policy dummies. To address
this, we repeat the analysis but augment (2) with controls for borough specific linear
time trends. Columns 4 to 6 in Table 4 present the results for each male age cohort when
time trends are conditioned on. We find that for the two older male age cohorts,
hospitalization rates are significantly higher in Lambeth relative to the rest of London
comparing the post- and pre-policy periods. Hence policy impacts remain even once linear
within borough time trends are controlled for, although we note the descriptive evidence
in Fig. 1 does not provide compelling evidence that such time trends should necessarily be
controlled for. In summary the evidence suggests that there are significant impacts of the
police policy of depenalizing cannabis on public health, as measured in hospitalization
rates for Class-A related drug use. These impacts are quantitatively large, apply to more
than one male age cohort, and are observed well after the policy depenalizing the
possession of cannabis is officially ended. To be clear, these results cannot be
interpreted as suggesting that there are some individuals that start taking Class-A drugs
as a result of the depenalization of cannabis. All we can infer is that there are
individuals, who prior to the policy might either have not been consuming illicit drugs at
all, or were consuming them in quantities that did not lead to hospitalization, who are
then in the longer term post-policy, significantly impacted by the depenalization policy
so as to require hospitalization for diagnoses related to Class-A drug use.

<hs>  Robustness checks</hs>
  ~~~~~~~~~~~~~~~~~

We now present evidence to underpin the credibility of the difference-in-difference
research design. These relate to probing the data to: (i) check for pre-existing divergent
trends in hospitalization rates between Lambeth and other London boroughs; (ii) evaluate
the robustness of the results to alternative control boroughs to compare Lambeth to; (iii)
examine whether differential changes over time in health care provision between Lambeth
and other locations, or other policies impacting hospitalizations for Class-A drug use,
could confound the results, and; (iv) shed light on whether individuals changed borough of
residence in response to the policy.

     <hss>Pre-trends</hss>

        The research design implicitly assumes that in the absence of the depenalization
        policy, there would have been no natural divergence/convergence in admission rates
        between Lambeth and the rest of London. The previous set of specifications that
        allowed for borough specific time trends already partly addressed this concern. A
        second way to address the issue is to exploit the four years of panel data prior
        to the introduction of the depenalization policy, from 1997 Q2 until 2001 Q2,
        using this period to test whether there is any evidence of a divergence in trends
        in hospitalization rates between Lambeth and the rest of London pre-policy. To do
        so, we estimate a specification analogous to Eq. (2) in the pre-policy sample but
        allow for only one split of the sample, midway through the pre-policy period. We
        then test whether there are divergent trends across Lambeth and the rest of London
        in admission rates between the first and second halves of the pre-policy period.
        As Table A5 shows (and consistent with the descriptive evidence in Fig. 1), for
        all male age cohorts this pre-policy sample split dummy interaction is not
        significantly different from zero suggesting that hospitalization rates in Lambeth
        are not diverging from London in the years prior to the depenalization policy. As
        discussed in Section 2, this is very much in line with the policy discussion
        around the underlying motivation for the policy, that emphasized the policy
        enabling the police to reallocate their effort towards non-cannabis crime, and
        which hardly mentioned the potential impacts on public health. Hence the data
        supports the assertion that the depenalization policy was not introduced
        specifically into Lambeth because of worsening public health related to drug-
        related hospital admissions. Nor is there any evidence of reversion to the mean in
        hospitalization rates with Lambeth converging back towards London-wide averages.
        In short, any form of ‘Ashenfelter dip’ does not appear to be confounding the
        estimated parameters, as was also suggested by the descriptive evidence in Fig. 1.

     <hss>Control boroughs</hss>

        We now examine the robustness of the findings to comparing Lambeth to other
        subsets of boroughs, rather then all boroughs London-wide (excluding only the
        immediate neighbors of Lambeth). To begin with, we follow on from the descriptive
        evidence in Fig. 1B and compare Lambeth to a more limited set of nine other London
        boroughs with similarly high levels of hospital admission rates for Class-A drugs
        pre-policy. As shown in Columns 1–3 of Table A6, with this restricted comparison
        sample of boroughs to Lambeth, there remains a significant impact of the policy
        among males aged 25–34 on the eve of the policy, an effect significant at the 1%
        level. The point estimate of the impact (.104) is actually larger than the
        corresponding coefficient in the baseline specification (.075), as reported in
        column 2 of Table 4. The remaining columns in Table A6 then show this result to be
        robust to alternative modifications to the control group of boroughs included: (i)
        boroughs with the very highest pre-policy admissions related to Class-A drugs
        (Columns 4–6, restricting the sample to four boroughs); (ii) including neighbors
        to Lambeth in the control group where spillovers in hospital admissions might have
        been greatest (Columns 7–9, expanding the sample to 32 boroughs). Along similar
        lines, the remaining columns in Table A6 consider restricting the control group of
        boroughs to those in which there exists: (i) a mental health trust headquarters
        (there are six such boroughs including Lambeth); (ii) a teaching hospital (there
        are eight such boroughs including Lambeth).21 The intuition for these comparisons
        is that residents of such boroughs might have access to especially high levels of
        quality in hospital care, or similar degrees of specialization in dealing with
        mental health disorders associated with the use of illicit drugs as in Lambeth
        where one mental health trust is headquartered. In line with the baseline results,
        we see that there were significant impacts on hospitalization rates post-policy in
        Lambeth for the youngest two age male cohorts in both these restricted samples.
        Taken together, these comparisons suggest that our baseline results are not driven
        solely by differences in health care between Lambeth and other London boroughs.

     <hss>Supply side changes and other confounders</hss>

        To provide further evidence on whether changes on the supply side of health care
        could be driving the difference-in-difference estimates, we utilize information in
        the HES administrative records both on the borough of residence of the individual,
        and the borough of treatment for each hospital episode. We then construct the time
        series for the percentage of men treated for a Class-A related diagnoses in a
        Lambeth health facility (by age cohort), that actually reside in Lambeth. To be
        clear, nearly all London boroughs have a hospital in them (with a handful of
        boroughs containing two). However, the specialist services required to treat
        diagnoses involving the use of Class-A drugs, such as those relating to mental
        health, are more concentrated in a small subset of facilities that are more
        dispersed across London. Each of these specialist facilities would be expected to
        treat patients from across London. If such services expanded in Lambeth during the
        post-policy period and were especially targeted towards Lambeth residents, then we
        would expect to observe, over time, a greater share of individuals treated in
        Lambeth to also reside in Lambeth. Fig. 2 presents the relevant time series
        evidence on this, again split by male age cohorts where ages are defined on the
        eve of the policy. Within each cohort, we find no evidence of changes in this
        percentage over time: for all male cohorts, between 30 and 40% of admissions into
        hospital are from individuals that are residents of Lambeth, and this does not
        change much over time. This evidence suggests that even if medical capacity were
        expanding in Lambeth, it did not lead to a differential treatment of Lambeth
        residents versus non-residents for the diagnoses related to Class-A drug usage we
        focus on in our main analysis.22 There are other potential confounding factors to
        consider. First, if the LCWS policy allowed the policy to reallocate their effort
        towards crime involving Class-A drugs, then the impacts we have documented would
        not solely be occurring through any demand side linkage between the use of
        cannabis and Class-A drugs (whether it arises from unobserved heterogeneity or
        state dependence via a gateway effect). However as discussed in Section 2, the
        body of evidence presented in Adda et al. (2013) suggests that the LCWS policy did
        not lead to a reallocation of police resources towards crime related to Class-A
        drug crime (rather, the police used the policy to reallocate their effort towards
        non-drug crime). Hence, in the current study, any link between the depenalization
        policy and hospitalizations for Class-A diagnoses most likely stems from the
        interlinkages between the demand sides of the markets for cannabis and Class-A
        drugs. A second potential confounding factor is that between January 2004 and
        January 2009 cannabis was declassified from a Class-B drug to a Class-C drug
        throughout the UK. This declassification effectively decriminalized the possession
        of small quantities of cannabis for personal use, mirroring the LCWS policy
        experiment in many ways.23 Such a nationwide policy would obviously only bias the
        difference-in-difference estimates that we focus on if its impact differed between
        Lambeth and other London boroughs. To show the policy impacts that we have
        documented between Lambeth and other London boroughs likely stem from the
        localized depenalization policy that only operated in Lambeth, we re-estimate our
        baseline specification (2) using only data running up to 2003 Q4, so up to the
        point where the nationwide policy change occurred. The result in Columns 1–3 of
        Table A7 show that for two out of three male age cohorts, there are significant
        impacts on hospitalization rates for Class-A related diagnoses in Lambeth, even
        over this restricted post-policy period before any changes in nationwide policy
        take hold.

     <hss>Residential mobility</hss>

        Throughout the analysis we have used the borough of residence at the time of
        admission to build hospitalization rates across cohorts. The documented increase
        in hospital admissions for Class-A drug related diagnoses in Lambeth following the
        introduction of the LCWS might then operate through two mechanisms: (i) a change
        in behavior of those residents in Lambeth prior to the policy; and (ii) a change
        in the composition of Lambeth residents, with the policy inducing a net inflow of
        people into the borough with a higher propensity for Class-A drug use.
        Undoubtedly, the geographical distances between London boroughs are small and
        travel costs are low relative to the fixed costs of permanently changing
        residence. Similarly the nationwide depenalization policy in place between 2004
        and 2009 would further have weakened incentives for individuals to relocate
        residence with Lambeth in response to the LCWS policy. However, if drug users
        perceive the depenalization of cannabis in Lambeth as signaling a wider weakening
        of police enforcement against all illicit drugs, there might be longer term
        benefits to relocating to the borough. Given the importance of assuming the
        underlying populations, and hence propensity for drug use, in Lambeth and the rest
        of London to remain unchanged over time in the difference-in-difference design, we
        now try to use the administrative records to shed some light on the extent to
        which drug users relocate their residence into Lambeth from other parts of London
        as a result of the depenalization policy.24 The HES data contain information on
        borough of residence for each individual admission to hospital, with individual
        identifiers allowing us to link patients across episodes and time. The major
        limitation of using hospital administrative records to shed light on changes in
        borough of residence in response to the policy, is that for those that are
        admitted only once during the study period, the data does not allow us to identify
        whether they have changed residence over time prior to the admission, or will do
        so subsequent to the admission. These individuals, that form the bulk of hospital
        admissions and that are included in the main analysis, cannot be included in the
        analysis below examining migration patterns. While this obviously limits our
        ability to shed light on the potential net migration into Lambeth of drug users in
        response to the depenalization policy, we know of no data set representative at
        the London borough level, that would match both changes in residence over time
        with individual hospital admissions or health outcomes over time. We therefore
        proceed by documenting changes in borough of residence for those that have at
        least two admissions into hospital between 1997 and 2007. To get a sense of the
        sample selection this induces, we note that in the pre-policy period, 326,683 men
        are admitted into hospital for any diagnosis, of which 10.6% are re-admitted (at
        least once) somewhere in London during the one-year period in which the LCWS
        policy is in place, and 25.3% are re-admitted (at least once) anytime in the post-
        policy period. Among those 1746 individuals admitted for Class-A drug related
        diagnosis in the pre-period, only 14.7% are observed being re-admitted for any
        diagnosis during the policy period, and 28.2% are observed being re-admitted for
        any diagnosis during the post-policy period. If individuals are induced to migrate
        to Lambeth in response to the depenalization policy, they might do so at some
        point during its actual period of operation between June 2001 and July 2002. To
        check for this, we first focus on those 1630 individuals that are admitted to
        hospital for any diagnosis in Lambeth during the policy period, and that are
        observed having at least one prior hospital admission somewhere in London pre-
        policy. Of these 1630 individuals, 1.7% are admitted for Class-A related diagnosis
        in Lambeth during the policy period. These are perhaps the most likely individuals
        to have moved to Lambeth in specific response to the depenalization policy.
        However we note that among this group, almost all their earlier pre-policy
        admissions (for any diagnosis) occur in Lambeth, so that there is no strong
        evidence of these individuals having recently moved to Lambeth during the policy
        period. While these results focus on those admitted for Class-A drug related
        diagnosis in Lambeth during the policy period, it might well be the case that drug
        users that migrate into Lambeth because of the policy are first admitted for some
        other diagnosis. Hence, we next focus on the 98.3% of hospital admissions in
        Lambeth during the policy period for any diagnosis unrelated to Class-A drug
        usage. Among these individuals, nearly all of them are observed with all their
        earlier admissions in Lambeth; only 10.3% have their last prior admission in some
        other borough, indicating that they changed their borough of residence at some
        point between their last admission and the end of the policy period. Taken
        together, these two pieces of evidence show that among those men with at least two
        hospital admissions since 1997, there is very limited evidence of there being
        significant changes of residence into Lambeth during the formal policy period
        between June 2001 and July 2002. Our next set of results examines longer term
        patterns of changes in borough residence. Given the fixed costs of changing
        residence and that in the post-policy period policy enforcement in Lambeth
        remained somewhat different than other boroughs, it might be reasonable to assume
        that a net inflow of drug users into Lambeth simply takes some time to occur. To
        check for this we examine whether inflows into Lambeth from other London boroughs
        change between two four-year windows: the first four year window occurs entirely
        pre-policy from April 1997 to April 2001, and the second four year window occurs
        entirely post-policy from April 2003 to April 2007. In each window we check
        whether among those admitted to hospital at least twice in the four-year window,
        and, where at least one admission relates to a diagnosis indicating Class-A drug
        use, whether changes in borough of residence between the first and last admission
        vary over time. In the first four-year pre-policy window from 1997 to 2001 we
        observe: (i) of those that have their first admission outside of Lambeth, 1.4% are
        observed with a later admission in Lambeth; (ii) of those that have their first
        admission in Lambeth, 16% are observed with a later admission outside of Lambeth.
        Doing the same for the later four-year window from 2003 to 2007 to see if this
        pattern of migration is altered in the longer term, we find that: (i) of those
        that have their first admission outside of Lambeth, 3.0% are observed with a later
        admission in Lambeth; and (ii) of those that have their first admission in
        Lambeth, 30% are observed with a later admission outside of Lambeth. Hence there
        is evidence of more frequent changes of residence among this subsample post-
        policy, but that this increase occurs both into Lambeth and from Lambeth: the
        inflow into Lambeth from other boroughs in the post-policy window relative to the
        pre-policy window increases (3.0% relative to 1.8%), but this is offset by the
        percentage increase in outflows from Lambeth to other boroughs among such
        individuals (30% relative to 16%).25 Overall this suggests is that, among those
        with multiple hospital admissions, there is increased mobility of residents across
        boroughs over time, but there is no strong evidence of systematically increased
        inflows into Lambeth over the second four year window relative to the first.

<h>EXTENDED RESULTS</h>
----------------

We now consider four margins of policy impact in more detail: the dynamic responses within
age cohorts over time, the heterogeneous impacts within age cohorts by previous admission
history, spillover impacts onto hospital admissions for alcohol-related diagnoses, and the
severity of hospital admissions. Establishing the existence and magnitude of each effect
is important to feed into any assessment of the overall social costs of this localized
change in drug enforcement policy related to the market for cannabis.

<hs>  The dynamics of the response</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

On longer term dynamics, Fig. 3 shows that for each cohort there is an inverse-U shaped
pattern of dynamic responses across time in the post-policy period. For each cohort the
depenalization policy has no significant impact on hospitalization rates during the policy
period, and estimated impacts increase thereafter for some time before starting to
decline. In line with the evidence in Table 4, the magnitude of the impacts are largest
for those in the younger two cohorts aged 15–24 and 25–34 on the eve of the policy. For
these age cohorts: (i) the impacts on hospitalizations related to Class-A drug use take a
year or two to emerge after the policy is first initiated; and (ii) the post-policy
impacts are the highest three to four years into the post-policy period, where the peak
impacts correspond to a near doubling of admission rates relative to the pre-policy period
for each cohort. Although the pattern of coefficients for the oldest cohort also follows
an inverse-U shape, the sign of the point estimates is quite different by the final period
considered: 4–6 years into the post-policy period, there is a significant and negative
impact on hospitalization rates. This might in part be driven by a different link between
the consumption of cannabis and Class-A for those in this age cohort. In comparison to the
literature linking policies regulating the market for illicit drugs and public health, all
of these dynamic responses are of significant duration. For example, Dobkin and Nicosia
(2009) study the impact of a government program designed to reduce the supply of
methamphetamine on hospitalization rates (by targeting precursors to methamphetamine), as
well as other outcomes. This policy is sometimes claimed to have been the DEA's greatest
success in disrupting the supply of an illicit drug in the US and indeed Dobkin and
Nicosia (2009) find that the policy had significant impacts on public health. However,
they document that these effects were short lived: within 18 months admission rates had
returned to pre-intervention levels. In contrast, the depenalization policy we document
has an impact on hospitalization rates that lasts at least 3–4 years post-policy for two
of the three male cohorts even though the policy itself is only formally in place for a
year.

<hs>  Admission histories</hs>
  ~~~~~~~~~~~~~~~~~~~

We next examine how the long run policy impacts are heterogeneous within the same age
cohort. To do so, we exploit the full richness of the administrative records to consider
differing impacts by individual histories of hospital admission for drug and alcohol-
related diagnoses during the pre-policy period from April 1997 to June 2001. This allows
us to shed light on whether those with a prior record of heavy substance abuse, respond
differentially to the depenalization of cannabis than does the rest of the population.
Relative to the existing literature linking drug enforcement policies and health,
exploiting this aspect of the data allows us to present novel evidence on the
characteristics of the marginal individuals most impacted by a policy of depenalizing
cannabis. Examining heterogeneous impacts along this margin is informative because
previous heavy users of illicit drugs might be engaged in habitual behaviors so there is
less scope for further increases in hospitalization rates for Class-A related diagnoses.
Hence the post-policy impacts are measured relative to the period in which the LCWS policy
is actually in place. Columns 4–6 in Table 5 consider policy impacts within each age
cohort among those that have a prior history of at least one hospitalization for drug or
alcohol-related diagnoses. The results suggest that in the longer term such cohorts are
either not affected by the depenalization policy, or for the oldest age cohort, their
admission rates significantly decline in Lambeth in the long term.26 Such long term users,
at least among the two younger cohorts, might be more habituated in their behavior and
less price sensitive to any change in the price of cannabis induced by the depenalization
policy. If so, this result would be consistent with the evidence based on NLSY97 data in
Deza (2011) who uses a dynamic discrete choice model to document that the gateway effect
from cannabis to hard drug use is weaker among older age cohorts. An obvious concern with
these results is that they might in part be confounded by natural time trends in
hospitalizations for Class-A drugs. These time trends might also differ across age groups
and by hospital admission histories. To address this, we repeat the analysis but augment
Eqs. (4) and (2) with controls for borough specific linear time trends. Table A8 presents
the results, again broken down for cohorts based on age and prior admission histories.27
The inclusion of borough specific linear time trends serves to reinforce the earlier
conclusions among those without a prior history of admissions (Columns 1–3, Table A8).
Among those with a history of admissions, we continue to find no impact among the two
youngest age cohorts, although among the oldest cohort the policy now has a positive and
significant impact on hospitalization rates.28

<hs>  Alcohol</hs>
  ~~~~~~~

There is an established body of empirical work examining the relationship between cannabis
and alcohol use: this has generated mixed results with some research finding evidence of
the two being complements (Pacula, 1998; Farrelly et al., 1999; Williams et al., 2004),
and other studies suggesting that the two are substitutes (DiNardo and Lemieux, 2001;
Crost and Guerrero, 2012; Anderson et al., 2013), or that there is no statistically
significant relationship between the two (Crost and Rees, 2013; Yörük and Yörük, 2013).
Many of these studies have identified these impacts among young people, sometimes
exploiting minimum legal drinking age that should create discontinuities in alcohol
consumption for those aged around 21. We provide a novel contribution to this debate by
examining the effect of depenalization on extreme forms of alcohol usage, leading to
hospitalizations. We do so for all three male age cohorts. As documented in the raw counts
data in Table 2, such admissions occur with far higher frequency for men in all age
cohorts, than admissions for either Class-A drugs or cannabis. Hence any positive or
negative impacts on admissions for alcohol can have dramatic implications for the monetary
health costs of the policy. Throughout, we measure admission rates for alcohol-related
diagnoses analogously to those used as our dependent variable in the baseline
specifications, Eq. (1). To begin with, we focus on admissions for alcohol-related
diagnoses where the primary diagnosis refers to alcohol. We exclude any admission that
additionally refers to the use of Class-A substances as the secondary cause of admission.
The results in Columns 1 to 3 of Table 6 show that there was a significant reduction in
alcohol-related admissions among the youngest cohort in Lambeth relative to the rest of
London, but there were no impacts on such alcohol-related admissions for older cohorts.
The result suggests that for the youngest age cohort, if depenalization causes the price
of cannabis to fall, then alcohol and cannabis might well be substitutes. The next set of
specifications probe further to examine the evidence of whether and how the policy impacts
the combined use of alcohol and Class-A drugs: here we define admission rates where the
primary diagnosis is again for alcohol-related diagnosis, but the secondary diagnosis
refers to the use of Class-A drugs. We find no evidence that the policy causes such
combined admissions to change in the longer term (and this occurs against a backdrop of
London-wide increases in such combined diagnosis admissions). Again, if the depenalization
of cannabis caused increased cannabis and Class-A drug use in the longer term, this last
set of results supports the assertion that such substances are not being used together, at
least among those most prone to extreme abuse of such substances.

<hs>  Severity of hospital admissions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

A final dimension along which to consider policy impacts relates to the severity of
hospitalizations, as measured by the number of days the individual stays in hospital for,
conditional upon admittance. This margin is of policy relevance because it maps directly
into the resultant healthcare costs associated with the depenalization of cannabis, as
calculated in the next section. We therefore first document how the length of individual
hospital episodes for diagnoses related to Class-A drug use changes differentially between
Lambeth and other London boroughs post-policy relative to the pre-policy period. To do so,
we estimate a specification analogous to Eq. (2) but where the dependent variable is the
individual length of hospital stay in days and the sample is confined to episodes where
the primary diagnosis relates to Class-A drugs. We focus on the first episode for any
hospital stay (that is the same as the entire hospital stay for 93% of observations), and
to avoid the results being driven by outliers, we drop observations where the length of
the stay is recorded to be longer than 100 days (that excludes a further 2% of all
stays).29 As the outcome variable now relates to individual outcomes (rather than borough-
quarter-year aggregates), we cluster standard errors by borough to capture unobservables
determining the length of hospital stays that are assumed correlated across residents of
the same borough. Columns 1 to 3 in Table 7 present the results, again split by age
cohort. The data suggests that in the longer term post-policy, across all three age
cohorts, the length of stay for Class-A drug related admissions significantly increases in
Lambeth relative to the London average. For example, among the 15–24 age cohort, hospital
stays increased by 3.7 days, and this is relative to a baseline pre-policy hospital stay
length of 7.2 days, an increase of 49%. The proportionate changes for the other age
cohorts are 29% for the 25–34 age cohort and 20% for the oldest age cohort. Hence, the
proportionate changes in length of hospital stay are greater for the age cohorts that were
younger at the time the depenalization policy was introduced. This emphasizes that quite
apart from the impacts of the depenalization of cannabis on hospitalization rates for
Class-A diagnosis that has been the focus of our analysis so far, the policy also has
impacts on the severity of those admissions for Class-A drug use. Both margins are
relevant for thinking through the public health costs of the policy as detailed in the
next subsection. We note further that the coefficients in the third row of Table 7 show
that in other London boroughs there are negative time trends in the duration of such
individual hospitalizations conditional on all other controls in Eq. (2). Hence the
findings for Lambeth post-policy do not appear to be driven by some systematic lengthening
of hospital stays for such diagnosis that might be occurring more generally across London.

<h>THE PUBLIC HEALTH COSTS OF THE DEPENALIZATION POLICY</h>
----------------------------------------------------

We use published the National Health Service estimates of the cost per hospital bed-day.30
This cost is comprised largely of hospital ward costs (nursing, therapies, basic
diagnostics and overheads), hence there is actually little variation by diagnosis: the
average cost per additional bed-day across all adult inpatient diagnoses categories is
£240 (Department of Health, 2012), but the upper end of the hospital bed-day costs,
relating to those for adult acute (inpatient) mental health stays, are only slightly
higher at £295 (PSSRU, 2011). We therefore use a figure between these estimates, of £250
per hospital bed-day, as quoted by the NHS Institute (2012). This likely represents a
lower bound of the true cost of a hospital bed-day because it does not include any
specific treatment costs or the additional costs from any associated stay in intensive
care.31 We then take our estimates from Tables 2 and 7 for each age cohort to calculate
each component of Eq. (7). For the youngest age cohort of those 15–24 on the eve of the
depenalization policy, ∆Hbc = 27.2 bed-days per quarter; of this total change, 24.1 bed-
days operate through the first channel of increased hospitalization rates, and 4.1 bed-
days through the second channel of longer hospital stays conditional on admission. Among
those aged 25–34 on the eve of the policy, ∆Hbc = 52.5 bed-days per quarter, where the
first channel corresponds to an increase of 42.6 bed-days, and the second component
generates an increase of 9.9 bed-days. Finally, for the oldest cohort of 35–44 year olds,
∆Hbc = − 26.9 bed-days per quarter, where the point estimate in the third row of Table 2
implies a decrease in hospitalization rates post-policy of 30.7 bed-days (although this
point estimate was not statistically different from zero), and this is only partially
offset by the increase through the second channel of 3.8 bed-days. Applying the estimated
costs per hospital bed-day of £250 to the change in the total number of hospital bed-days
per quarter, for each cohort in Lambeth in the post-policy period on average, reveals the
increased public health cost to be: (i) £6802 among those aged 15–24 on the eve of the
policy; and (ii) £13,136 among those aged 25–34 on the eve of the policy. Summing across
four quarters we derive the conservative public health cost of the depenalization policy
to be £79,752 per annum, on average across all the post-policy years in the sample.
Aggregating these cohorts across four quarters then suggests the natural decrease in costs
associated with hospital bed-days is £4935. Hence the increase in bed-days attributable to
the policy more than offsets this natural decrease in hospital bed-days attributable to
London-wide time trends. Of course, this calculation still underestimates the total public
costs of the increased hospital bed-days within Lambeth due to the policy because of the
existence of many additional channels that we have ignored. First, we have ignored any
additional demands placed on other parts of the national health service unrelated to
hospital inpatient stays, as a result of the depenalization policy. These include demands
through outpatient appointments, hospital emergency departments, and through treatment
centers. Indeed, the existing evidence from the US on the link between the availability of
cannabis and health relate to emergency or treatment costs: Model (1993) find that the de
facto decriminalization of cannabis in twelve US states from the mid-1970s significantly
increased cannabis-related emergency room admissions. Chu (2012) similarly finds that the
passage of US state laws that allow individuals to use cannabis for medical purposes leads
to a significant increase in referred treatments to rehabilitation centers. Second, we
have ignored any cost to individual users of being hospitalized. Such events almost surely
impact individual welfare, especially given the robust association found across countries
in the gradient between health and life satisfaction.

<h>DISCUSSION</h>
----------

We evaluate the impact of a policing experiment that depenalized the possession of small
quantities of cannabis in the London borough of Lambeth, on hospital admissions related to
illicit drug use. Despite health costs being a major social cost associated with markets
for illicit drugs, evidence on the link between how such markets are regulated and public
health remains scarce. Our analysis provides novel evidence on this relationship, at a
time when many countries are debating moving towards more liberal policies towards illicit
drugs markets. We have exploited administrative records on individual hospital admissions
classified by ICD-10 diagnosis codes. We use these records to construct a quarterly panel
data set by London borough running from 1997 to 2009 to estimate the short and long run
impacts of the depenalization policy unilaterally introduced in Lambeth between 2001 and
2002. We find that the depenalization of cannabis had significant longer term impacts on
hospital admissions related to the use of hard drugs. Among Lambeth residents, the impacts
are concentrated among men in younger age cohorts. The dynamic impacts across cohorts vary
in profile with some cohorts experiencing hospitalization rates remaining above pre-
intervention levels three to four years after the depenalization policy is first
introduced. We combine these estimated impacts on hospitalization rates with estimates on
how the policy impacted the severity of hospital admissions to provide a lower bound
estimate of the public health cost of the depenalization policy. Our analysis contributes
to the nascent literature evaluating the health impacts of changes in enforcement policies
in the market for illicit drugs. The depenalization of cannabis is one of the most common
forms of such policy either implemented (such as in the Netherlands, Australia and
Portugal) or being debated around the world (such as in many countries in Latin America).
The practical way in which the localized depenalization policy we study was implemented is
very much in line with policy changes in other countries that have changed enforcement
strategies in illicit drug markets and as such we expect our results to have external
validity to those settings. However unlike those settings, we are able to exploit a
(within-city) borough level intervention and so estimate the policy impacts using a
difference-in-difference design, as well as exploring differential impacts across
population cohorts, where cohorts are defined by gender, age, previous admissions history,
and borough of residence. This is different from much of the earlier research that, with
the exception of studies based on US or Australian data, can typically only study
nationwide changes in drug enforcement policies such as depenalization, and have therefore
had to rely on time variation alone to identify policy impacts (Reuter, 2010). The
administrative records we exploit allow us to provide novel evidence on how the impacts of
such policies vary across population cohorts, over time within a cohort, and how they
interact with potential changes of residence of drug users. Clearly, such policy impacts
are unlikely to ever be estimated using randomized control trial research designs. We have
used a difference-in-difference research design exploiting an unusual policy experiment in
one London borough that allows us to exploit within and across borough differences in
health outcomes to identify policy impacts. The key concern with such a research design is
to distinguish policy impacts from time trends. To do so, we have used the detailed
administrative records to present evidence on how different cohorts (by gender, age and
previous admission history) are differentially impacted by the policy, how the results are
strengthened when controlling for time trends, and checked for the presence of trends in
the pre-policy period. Our results suggest policing strategies have significant, nuanced
and lasting impacts on public health. In particular our results provide a note of caution
to moves to adopt more liberal approaches to the regulation of illicit drug markets, as
typically embodied in policies such as the depenalization of cannabis. While such policies
may well have numerous benefits such as preventing many young people from being
criminalized (around 70% of drug-related criminal offenses relate to cannabis possession
in London over the study period), allowing the police to reallocate their effort towards
other crime types and indeed reduce total crime overall (Adda et al., 2013), there remain
potentially offsetting costs related to public health that also need to be factored into
any cost–benefit analysis of such approaches. Two further broad points are worth
reiterating. First, our analysis relates to the more general study of the interplay
between the consumption of different types of drug. In particular there is a large
literature testing for the “gateway hypothesis” that the consumption of one “soft” drug
causally increases the probability of subsequently using a “harder drug”. The crucial
challenge for identification is the potential for unobserved factors or heterogeneity that
could drive consumption of multiple types of drug. Existing work has tried to tackle this
problem by either: (i) instrumenting the gateway drug with a factor unrelated to the
underlying heterogeneity, typically using cigarette and alcohol prices (Pacula, 1998;
DiNardo and Lemieux, 2001; Beenstock and Rahav, 2002); or, (ii) using econometric
techniques to model the possible effects of unobserved heterogeneity (Pudney, 2003; van
Ours, 2003; Melberg et al., 2010). To be clear, in our analysis we make no attempt to test
for gateway effects directly, but our contribution to this literature is to demonstrate
that the markets for cannabis and hard drugs are concretely linked — be it because of
gateway effects or some other channel — so that changes in policy that affect one market
will have important repercussions for the other (DeSimone and Farrelly, 2003; van Ours and
Williams, 2007; Bretteville-Jensen et al., 2008). Finally, our analysis highlights the
impact that policing strategies can have on public health more broadly. It is possible
that other policing strategies, such as police visibility or zero-tolerance policies,
could also have first order implications for public health. These effects could operate
through a multitude of channels including: (i) police behavior directly impacting markets
and activities that determine individual health, such as the case studied in this paper;
and (ii) police behavior affecting perceptions of crime and thus influencing psychic well-
being. This possibility opens up a rich area of further study at the nexus of the
economics of crime and health.


<h>REFERENCES</h>
----------

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<ART>Policy experimentation, political competition, and heterogeneous beliefs
========================================================================

Authors: Antony Millner, Hélène Ollivier, Leo Simon
DOI: 10.1016/j.jpubeco.2014.08.008
Year: 2014  |  Pages: 84-96
ASJC codes: 2002, 2003
Keywords: Beliefs, Learning, Political economy

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We consider a two period model in which an incumbent political party chooses the level of a current policy variable unilaterally, but faces competition from a political opponent in the future. Both parties care about voters' payoffs, but they have different beliefs about how policy choices will map into future economic outcomes. We show that when the incumbent party can endogenously influence whether learning occurs through its policy choices (policy experimentation), future political competition gives it a new incentive to distort its policies - it manipulates them so as to reduce uncertainty and disagreement in the future, thus avoiding facing competitive elections with an opponent very different from itself. The model thus demonstrates that all incumbents can find it optimal to 'over experiment', relative to a counterfactual in which they are sure to be in power in both periods. We thus identify an incentive for strategic policy manipulation that does not depend on parties having conflicting objectives, but rather stems from their differing beliefs about the consequences of their actions.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Many of the most important public policy problems democratic countries face require
cumulative efforts by successive governments to be successfully managed. Consider
environmental policy (in particular regulation of stock pollutants such as greenhouse
gases), social security reform, sovereign debt management, and public infrastructure
development. None of these issues can be tackled in a single legislative term, and the
total quantity of resources devoted to them will likely be the result of decisions taken
by several governments. As such, the policies incumbent political parties choose to
address these issues are heavily influenced by the incentives that the political system
provides for them to make sound ‘long-run’ policy decisions, even if the effects of those
decisions may only be realized once they have left office. The lack of future political
control that is characteristic of democratic systems means that, for the purposes of
setting ‘long-run’ policies, incumbents have incentives to manipulate their current policy
choices so as to influence both who gets elected in the future and the policy choices
future governments will make (Persson and Svensson, 1989; Aghion and Bolton, 1990;
Tabellini and Alesina, 1990; Milesi-Ferretti and Spolaore, 1994; Besley and Coate, 1998;
Persson and Tabellini, 2000; Azzimonti, 2011). These strategic incentives exist even if
parties are not purely office seeking, but have interests that coincide with those of a
group of voters, e.g. in models of partisan politics. These effects have traditionally
been studied in models with heterogeneous preferences: parties are assumed to have
intrinsically different preference parameters, which induce heterogeneous preferences over
policies, and hence a strategic incentive for an incumbent party to manipulate present
policy choices given that its reelection is uncertain. While heterogeneity in preference
parameters undoubtedly accounts for some of the divergences between political parties’
preferred policies, heterogeneity in beliefs is likely to be an equally important factor.
Milton Friedman famously argued that “differences about economic policy among
disinterested citizens derive predominantly from different predictions about the economic
consequences of taking action…rather than from fundamental differences in basic values”
(Friedman, 1966). More recently, public surveys in the US demonstrate a strong
polarization in the beliefs of Democrats and Republicans about a variety of policy issues,
including, for example, the likely causes and severity of climate change (Leiserowitz et
al., 2012; Borick and Rabe, 2012). Despite the empirical plausibility of belief
heterogeneity, the consequences of relaxing the common prior assumption have been largely
unexplored in the political economy literature on strategic policy choice.2 The crucial
new feature of political competition induced by heterogeneous beliefs is that beliefs are
dynamic, and potentially endogenous. Parties' policy preferences may change over time as
their beliefs evolve in response to new information. Moreover this learning process may,
at least to some extent, be under the control of the incumbent, who may choose policies
with the express purpose of revealing information about their consequences in the future;
learning may be ‘active’. Active learning — the idea that current policy choices influence
how much is learned in the future — is an old concept in economics (e.g. Prescott, 1972;
Grossman et al., 1977), which has been applied to problems in monetary policy (Bertocchi
and Spagat, 1993), environmental regulation (Kelly and Kolstad, 1999), and firm behavior
(Keller and Rady, 1999). It can be seen as a form of experimentation — we choose an
action, observe its consequences, and so learn something new about the relationship
between choices and outcomes. In addition, it is often the case that the more intensely we
pursue a policy, the more we can separate the ‘signal’ from the ‘noise’, and the more we
learn about its effects.3 Thus when learning is active, and parties have divergent beliefs
that they update rationally, the incumbent party has a measure of control over its own,
and its opponent's, future policy preferences. This gives rise to strategic incentives for
policy manipulation that are entirely absent when parties merely have different preference
parameters. Our core contribution is to elucidate the interaction between belief
heterogeneity, active learning (or experimentation), and political competition, and how
this affects the size of public programs with uncertain deferred benefits (or costs). We
focus on how the interaction between these factors determines an incumbent's response to
the intertemporal tradeoff inherent in such problems. We thus abstract from questions of
taxation and redistribution, and consider a stylized model in which voters differ only in
their beliefs about the benefits of the policy, and parties that represent the beliefs of
groups of voters must decide only on the level of some policy variable. We show that the
interaction between active learning and political competition gives rise to a new
incentive for incumbents to distort their policy choices. This incentive pushes incumbents
to choose policies that increase their chances of resolving uncertainty in the future,
regardless of their beliefs: they will over experiment. The intuition behind this result
is simple — since the preferences of parties with different a priori beliefs converge when
learning occurs, incumbents avoid future competitive elections with an opponent very
different from themselves by choosing policies that reduce disagreement. We demonstrate
this mechanism in a two period model that combines the literature on intertemporal
decision making under uncertainty and learning (Arrow and Fisher, 1974; Henry, 1974;
Epstein, 1980; Gollier et al., 2000), with a simple but flexible model of political
competition (Wittman, 1973, 1983; Roemer, 2001). To demonstrate the effects cleanly, the
model assumes that parties care only about the voters' well-being, and disagree only in
their beliefs. Thus, in the absence of belief heterogeneity all parties in our model would
agree on the correct policy choice, which would also be the optimal policy for the voters.
Yet even in the sanguine case where parties are well intentioned and have common
objectives, heterogeneous beliefs and political competition will distort their policy
choices. We show that when learning is active enough, all incumbents will over-experiment
relative to a counterfactual in which they are sure to be in power in the future,
regardless of their beliefs and the beliefs of their political opponents. Section 2 sets
out the model structure. Section 3 examines how the interaction between active learning
and political competition affects policy choices when beliefs are heterogeneous, without
specifying the actual form of the political competition between parties. To build
intuition, a simple model with binary policy choices is discussed first, followed by a
more complex model with continuous policy choices. Section 4 specializes to a specific
model of political competition: the Wittman model. In our version of this model parties
know the distribution of the voters' beliefs, voters vote for their preferred platform,
and elections are decided by majority rule. We show that our results hold under plausible
primitive conditions on the parties' payoff functions in this case, which apply in both
‘full commitment’ and ‘no commitment’ versions of the model. We reflect on the application
of our results to a variety of policy issues in Section 5, before concluding.

<hs>  Related literature</hs>
  ~~~~~~~~~~~~~~~~~~

While the consequences of heterogeneous beliefs and strategic experimentation for the
policy choices of incumbents are (to the best of our knowledge) unexplored, several papers
investigate some of these factors in other contexts. Piketty (1995) considers a model of
social mobility and redistributive taxation, in which agents hold different beliefs about
the relative importance of effort and social class in determining economic outcomes. The
beliefs of different agents are updated based on their income mobility experience, and
transmitted to their descendants. Piketty shows that belief heterogeneity persists in the
steady state, and that experience of income mobility, and not simply income level,
contributes to forming political attitudes. While heterogeneous beliefs are at the core of
this work, it focusses on the voters' belief formation processes, and not on strategic
policy experimentation by incumbent governments. Strulovici (2010) is explicitly concerned
with strategic experimentation, but focusses on strategic voters, rather than strategic
parties. In his model pivotal voters recognize that experimentation reduces their
likelihood of being pivotal in the future — this results in under-experimentation in
equilibrium. We focus on the behavior of strategic parties that manipulate their current
policies in part to influence the beliefs of future voters. In contrast to Strulovici
(2010), we show that when parties have good faith disagreements with their political
opponents, they have an incentive to over experiment. Callander and Hummel (2013) consider
a model that is in some respects close to ours. They examine the efficiency of political
turnover, when the only link between successive governments is the information they
possess. Incumbents can experiment strategically to influence the information that their
successors will use to make their policy choices. They show that, due to the time
inconsistency issues that are inherent in political systems with turnover, experimentation
can improve the efficiency of policies, as it creates a channel for intertemporal
influence. This informational channel of influence is also present in our work, but the
political context differs. Parties have common beliefs but heterogeneous objectives in
their model, and political turnover is imposed exogenously. By contrast, parties in our
model have common objectives but heterogeneous beliefs, and the identity of future
governments is determined endogenously via competitive elections. This allows us to study
the interaction between endogenous political competition, policy experimentation, and
heterogeneous beliefs. Finally, Hirsch (2013) considers a model of political organization
in which a principal and an agent disagree about which policy to implement, but share the
same objectives, and can engage in experimentation. Hirsch shows that it may be optimal
for the principal to defer to the agent to motivate him to act, or to demonstrate to the
agent that his beliefs are incorrect. While the fact that agents in his model differ only
in their beliefs is common to our analysis, the roles of the players are exogenously
assigned in his work. His model focusses on strategic delegation in a hierarchical
organization, rather than strategic interaction between political parties. Despite the
differences in context between our work and that of the last three papers mentioned above,
a common overarching theme unites them. In all these cases learning provides a channel for
influence, which is used to the advantage of a ‘first-mover’. In Strulovici (2010) this is
the pivotal voter, in Hirsch (2013) it is the principal, and in Callander and Hummel
(2013) and our own work, it is an incumbent government. Thus our work contributes to a
wider recent research program which sees information as a source of strategic control in a
variety of contexts.

<h>THE MODEL</h>
---------

We consider a two period model, and assume two political parties, indexed by i ∈ {G, B}.
The parties are well-intentioned: they care only about the voters' well-being, and don't
seek office for their own ends. Our choice of labels for the parties is motivated by an
environmental interpretation of the model (‘G’ = Green, ‘B’ = Brown) which we will use to
provide intuition at several points in the exposition, but the model is applicable much
more widely. In the first period the incumbent party sets some policy variable e1, which
gives rise to certain first period payoffs U(e1). Second period payoffs W(e2|e1, λ) depend
on the policy e2 that is implemented in the second period, on the legacy of first period
policy choices e1, and on an a priori uncertain parameter λ, which affects the optimal
second period policy. The conditions we impose on U and W will be discussed below, for now
we focus on the model structure. The function B(e) denotes known short-run benefits from
industrial processes that emit the pollutant, and C(e1 + e2) denotes long-run costs (e.g.
health impacts or productivity losses) resulting from the accumulation of the pollutant in
the atmosphere. The magnitude of these future costs is uncertain, and depends on the
realization of λ. Returning to our general model exposition, we assume that λ ∈ {λL, λH},
where λL < λH. The crucial feature of our model is that parties and voters have
heterogeneous beliefs about the consequences of policy choices. In the first period, party
i believes that λ = λL with prior probability qi. We assume without loss of generality
that qG < qB. In our environmental example, this implies that the Green party puts more
subjective weight on the ‘high damages’ state λ = λH than the Brown party — hence their
labels. The voting population's beliefs are also heterogeneous, and each party's beliefs
are assumed to be representative of some exogenously given subset of voters. The
heterogeneity in the parties' beliefs is the only difference between them. A∗(e1, q) is
thus the payoff a party with beliefs q expects to receive in the second period if the
value of λ remains unknown in the future, and it has exclusive control over which second
period policy is implemented. e2∗(e1, q) is the policy this party would choose in this
situation. The parties are dogmatic, in that they do what they think is best for the
voters given their beliefs qi, and don't account for the beliefs of those who disagree
with them when making their policy choices. They are however rational, and realize that in
the future new observations may be realized that provide information about the value of λ.
They will interpret this new evidence in a rational Bayesian fashion, and update their
priors. Moreover, each party knows that the other party will do the same. We compress this
incremental learning process into a single period. To keep the learning process simple we
assume that in the second period either the true value of λ is revealed (with probability
f(e1)), or nothing is learned about the value of λ (with probability 1 − f(e1)).4
Crucially, we allow the probability of learning to depend on first period policies. If
f′(e1) > 0 then learning is active — the more intensive are first period policies, the
greater the chance of learning the value of λ in the second period. In this case, policy
experimentation carries an informational payoff. Alternatively, if f′(e1) = 0, we say that
learning is passive: policy choices have no informational consequences. Fig. 1 illustrates
the timing of events in the model. At the beginning of the first period an incumbent
chooses a policy e1. At the end of the first period either the true value of λ is revealed
(with probability f(e1)), or nothing is learned (with probability 1 − f(e1)). If λ is
revealed, the parties' policy preferences are identical in the second period — there is no
difference between them as they hold the same beliefs. In this branch of the decision tree
there is a ‘trivial’ election in the second period — it doesn't matter who gets elected,
as both parties will choose the same policy. If however λ is not revealed, the parties'
beliefs remain divergent in the second period. In this case even though the parties have
common objectives, they offer different platforms, reflecting their different priors. Thus
each party announces a policy platform e2i at the beginning of the second period, and
voters decide between them in competitive elections.

<h>EFFECT OF POLITICAL COMPETITION AND ACTIVE LEARNING ON POLICY CHOICE</h>
--------------------------------------------------------------------

Our main hypothesis is that the interaction between active learning and political
competition gives rise to incentives for incumbents to ‘over experiment’ with their first
period policies. This reduces uncertainty and disagreement in the future, and hence avoids
costly political competition. In order to demonstrate this in our model, we need to
examine the additional effects of active learning, political competition, and their
interaction, on policy choice. Thus, we need to define baseline learning and political
scenarios which we will compare to the active learning/political competition scenarios. We
have thus set up two dimensions of variation in our model — passive vs. active learning,
and political competition vs. the individual optimum. Evaluating the optimal policies in
(10) and (13) under the two learning scenarios (11) and (12) leads to four policy
scenarios. Table 1 summarizes our notation for the optimal first period policies in these
four cases. The passive learning/individual optimum cases allow us to determine the
additional effects of active learning/political competition, relative to these baselines.
The interaction between active learning and political competition is captured by looking
for differences between the effect of active learning (relative to passive learning) in
the two different political scenarios.

<hs>  A simple model with binary policy options</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In order to build intuition, we consider a simple version of the above model in which the
first period policy e1 can take only two values: e1 ∈ {0, 1}.6 The incumbent must either
implement a policy (e1 = 1), or do nothing (e1 = 0) in the first period. Second period
policies e2 may be discrete or continuous — all that we require is that optimal second
period policies e2∗(e1, q) depend on the value of q. Active learning gives any incumbent
party an additional incentive to experiment (i.e. choose e1 = 1) relative to the passive
learning case, in both the individual optimum and political competition scenarios.
However, this additional incentive is greater under political competition than in the
individual optimum. The first of these inequalities follows from the convexity of the
‘max’ function (information has positive value), and the second from (9). Thus there is a
greater incentive to choose e1 = 1 when learning is active than when it is passive when
the incumbent faces political competition in the future. Similarly, there is a greater
incentive to choose e1 = 1 under active learning (relative to passive learning) when the
incumbent is certain to be in office in both periods. This result says that the difference
between the incumbent's incentive to choose e1 = 1 under active vs. passive learning is
larger when it faces political competition than in its individual optimum. There will thus
be cases in which switching from passive to active learning induces the incumbent to
switch from e1 = 0 to e1 = 1 under political competition, but not in the individual
optimum. The converse, however, can never happen. If a switch from passive to active
learning causes the incumbent party to change from e1 = 0 to e1 = 1 in the individual
optimum, it must also do so under political competition. This simple result illustrates
the incentive for the incumbent party to over experiment when it faces political
competition from an opponent who shares its goals, but has differing beliefs. While active
learning provides an additional benefit (relative to passive learning) to the e1 = 1
policy under both political scenarios, the difference between the relative benefits of e1
= 1 under active and passive learning is greater under political competition than in the
individual optimum. This is so since, under active learning, the incumbent party increases
its chance of avoiding an election with an opponent different from itself by choosing e1 =
1. It chooses its first period policy strategically to reduce disagreement in the second
period. This result relies critically on the fact that the parties have heterogeneous
beliefs. Beliefs are endogenous and amenable to manipulation, whereas preference
parameters are not.

<hs>  Continuous first period policies</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The positive interaction between active learning and political competition is easily
demonstrated in the binary case examined in Section 3.1. We now extend these results to a
continuous model of policy choice. This turns out to be a more complex problem, for the
following reason. The results we obtained in the binary model only required us to rank
payoff levels under the different scenarios. When first period policies e1 are continuous
(and payoffs W are non-linear in e1), the comparison between optimal first period policies
under different learning and political scenarios involves not only the levels of second
period payoffs, but also the derivatives of these payoffs with respect to e1. This
additional complexity has long been recognized in the literature on the effect of learning
on dynamic choice (e.g. Epstein, 1980; Ulph and Ulph, 1997; Gollier et al., 2000), which
has focussed on conditions that are sufficient to determine the direction of the change in
the optimal choice variable under different learning scenarios. Following in this
tradition, we will state sufficient conditions for an analogue of the intuitive results
obtained in the binary case to hold in a continuous model. To understand the conditions in
the proposition, it is helpful to begin by examining a special case. Suppose that W(e2|e1,
λ) is independent of e1. In this case the only way e1 influences second period payoffs is
through the effect it has on the probability of learning f(e1); it does not directly
affect the parties' payoffs in the second period. Thus the only linkage between the
periods is informational. In this case the conditions (18–19) are satisfied as equalities
as their constituent terms are all identically zero, and condition (20) is satisfied for
any strictly increasing f(e1), as its right hand side is zero. Thus the conclusions of the
proposition hold identically in this case (with political competition having no effect on
e1 under passive learning in conclusion (b)). In words, second period payoffs under
political competition when λ is unknown are always less than payoffs in the individual
optimum when λ is unknown, which are in turn always less than payoffs when λ is known in
the second period. These relationships imply the pattern of effects we observed in the
binary policy case (we used them in (15–17)), and these effects carry over to the
continuous policy case when information is the only linkage between the two periods. The
core insight is that in this special case our intuition for how the interaction between
active learning and political competition, which was based on comparisons of the levels of
payoffs under different scenarios, is undisturbed by the derivatives of payoffs. Comparing
these inequalities to those in (21), we see that the conclusions of Proposition 2 hold if
the derivatives of second period payoffs with respect to e1 are ranked in the same way as
the levels of the payoffs. While the message of the proposition is clear, the conditions
(18–19) depend on endogenous quantities, and it is thus not possible to know when they are
satisfied without putting more structure on the problem. This is a common feature of
learning models (see e.g. Epstein, 1980). In the next section we consider two common
models of political competition, and, in each, find primitive conditions on the payoff
function W(e1|e2, λ) that ensure that the crucial conditions (18–19) hold.

<h>SPECIFYING THE MODEL OF POLITICAL COMPETITION</h>
---------------------------------------------

In the model we consider, the voters' choices depend only on the platforms parties
announce (i.e. they don't have a party affiliation), and the distribution of their beliefs
is known to both parties. We consider two variants of the model — a full commitment case,
and a no commitment case — and show that the same primitive conditions on the payoff
function W(e2|e1, λ) imply that the conditions of Proposition 2 are satisfied in both
cases.

<hs>  A median voter model (full commitment)</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Thus when voters' beliefs are known and they have single peaked preferences, parties'
platforms converge completely in the second period — they both offer the median voter's
optimal policy.9 With this expression for the equilibrium value of the ‘no learning’ sub-
game, we can seek conditions on the payoff function W which ensure that (18–19) of
Proposition 2 are satisfied. The next result provides such conditions, without specifying
a parametric form for W. (26) is the standard concavity condition, and in addition we
assume that solutions to the second period optimization problem are interior, so that the
constraint e2 ≥ 0 is not binding. This assumption simplifies our analysis, but our results
are not crucially dependent on it. It is readily shown (see Appendix C) that the
conditions (27) and (28) imply respectively that the optimal second period policy e2∗(e1,
q), is decreasing in e1, and increasing in q. In our environmental example this implies
that the greater is the level of first period emissions, the less parties want to emit in
the second period, and similarly, the greater the weight they put on the low damages state
λL, the more they want to emit in the second period. This property has important
consequences for the condition (18), which gives rise to conclusion (b) of Proposition 1:
under passive learning any incumbent reduces e1 under political competition relative to
its individual optimum. This is really the novel condition of the proposition, as the
other condition (19), which guarantees that active learning causes incumbents to increase
e1 relative to passive learning, is well known; it can be seen as a special case of the
sufficient conditions for signing the effect of learning on policy choice derived in
Epstein (1980). Conclusion (b) is novel, so it is important to understand how the
properties of the payoff function in Proposition 3 give rise to it. This can be seen by
thinking about the strategic consequences of (34) in the political competition scenario,
as we now explain. Thus from the inequalities (35–36) and (37–38), we see that if we
increase e1, the distance between the median voter's optimum and either parties' optimum
increases. However, reducing e1 brings the median voters' optimum closer to both of the
parties' individual optima. Since it is the median voters' optimum that is implemented
under political competition, and all parties have single peaked preferences over second
period policies, all parties want this policy to be as close to their individual optima as
possible. Fig. 2 illustrates this intuition graphically. The condition (34) thus ensures
that regardless of whether the incumbent party's beliefs qi are greater or less than qm,
it always has a strategic incentive to reduce e1 relative to its individual optimum.

<hs>  Exogenous election probabilities (no commitment)</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We can treat all these cases at once by allowing the probability of election to be an
arbitrary constant. We have the following proposition: Suppose that the conditions on U
and W inProposition 3are satisfied. Assume that the outcome of the political process is
exogenously determined, so that πi(e2i, e2j) is an arbitrary constant in [0, 1]. Then the
conclusions ofProposition 3continue to hold. Thus the results in Section 4.1, in which the
election outcome was endogenously determined by the parties' platforms and parties were
assumed to commit, carry over to the case in which election outcomes are exogenous
(independent of the parties' platforms) and parties cannot commit.

<h>APPLICATIONS</h>
------------

The mechanism we have identified can be applied in many policy contexts. Before we discuss
some examples however, we emphasize that we see the effect we have highlighted as only a
partial contributing factor to actual policy outcomes. Our purpose has been to highlight
an informational channel of intertemporal influence and its effects on the policy choices
of incumbents. The model is intentionally idealized, in order to demonstrate the new
incentives for policy manipulation that belief heterogeneity gives rise to. Previous
literature (e.g. Persson and Svensson, 1989; Aghion and Bolton, 1990) examines strategic
policy choice when parties' objectives are heterogeneous but they have common beliefs; our
work assumes the opposite. The real world, of course, falls between these two stark cases.
As a first example of the application of our mechanism, consider the case of public
smoking bans. The benefits of reducing second-hand smoke include lowering the risk of lung
cancer, reducing health care costs, and improving worker productivity. The costs of bans
are born by restaurants and bars who may see a decline in profits. These costs are
uncertain before the policy has been implemented. Indeed, the impacts of smoking bans on
the restaurant business are still debated (Hyland et al., 1999; Adams and Cotti, 2007).
Given this uncertainty, and conflicting sources of information, different public
representatives are likely to hold different beliefs about the consequences of these laws.
Despite conflicting views, public officials have proven willing to experiment with smoking
bans, as their diffusion from a few cities and states (San Luis Obispo, California in
1990, California in 1998, New York City in 2002) to many states and countries illustrates
(Adams and Cotti, 2007; Eriksen and Chaloupka, 2007). Congestion charges provide another
application. These taxes provide an immediate social benefit by reducing traffic
congestion and improving air quality in city centers. However, they also impose a priori
uncertain costs on residents who commute to the city center by car, and hence on centrally
located retail businesses. Despite disagreements about the projected impacts of these
policies, city administrations have rolled them out. The charges are usually introduced in
an initial experimental phase, which enables affected parties to learn about their
consequences. This occurred in Stockholm in 2007, when the charge was implemented for an
initial seven month trial period, before being expanded and made permanent (Winslott-
Hiselius et al., 2009). Similarly, the London congestion charge in 2003 was adopted after
an 18-month public consultation period (Leape, 2006). A further example is provided by
policies that aim to regulate national emissions of atmospheric pollutants. Policies that
place an annual cap on emissions, such as the cap-and-trade mechanisms of the US Acid Rain
Program (established in 1990 to curtail sulfur dioxide and nitrogen oxide emissions), or
the European Emissions Trading Scheme (established in 2005 to reduce greenhouse gas
emissions), may reduce the future damages that arise from the accumulation of pollutants.
However, different political actors hold different beliefs about the magnitude of these
damages, which are highly uncertain (Borick and Rabe, 2012). Since forcing the atmospheric
system with emissions allows us to observe how it responds, emitting more today helps to
reduce uncertainty in the future (Kelly et al., 2005). Thus our model suggests that even
well-intentioned incumbents have an incentive to set less stringent caps than they would
prefer to, so as reduce uncertainty and disagreement in the future. Unlike more
conventional explanations of the difficulty of passing stringent abatement policies, which
appeal to partisan motives, collective action problems, and the influence of special
interest groups, this explanation does not require political parties to act solely in
their self-interest; it is simply a consequence of disagreements about matters of fact.

<h>CONCLUSIONS</h>
-----------

Our analysis has identified a novel incentive for incumbents to manipulate their policy
choices, when beliefs are the primary source of disagreement between political parties.
This stems from the interaction between active learning — the ability to endogenously
influence future information revelation through current policy choices — and political
competition. When learning is active incumbents can control the degree of disagreement in
the future. Since the incumbent party avoids a costly election with an opponent very
different from itself if information is revealed and beliefs converge, it has an incentive
to increase the chances of resolving uncertainty in the future, regardless of its initial
beliefs. This effect relies crucially on the fact that, unlike intrinsic preference
parameters, beliefs are endogenous, and thus subject to manipulation. The mechanism we
identify is widely applicable, and may have explanatory power for any policy issue about
which voters and parties have diverse beliefs, and where learning occurs through policy
implementation. Unlike conventional explanations of distortions to public good provision
due to the influence of politics, our result does not rely on rent-seeking and the
influence of special interest groups (Aidt and Dutta, 2007; Bohn, 2007; Battaglini and
Coate, 2008), or the institutional structure of government (Persson and Tabellini, 1999;
Lizzeri and Persico, 2001; Acemoglu and Robinson, 2001). It can be thought of as a
parsimonious causal mechanism that assumes the best of political actors, yet predicts that
they will still do more to reduce uncertainty than they would like to.


<h>REFERENCES</h>
----------

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  [9] Timothy Besley, Stephen Coate. Sources of Inefficiency in a Representative Democracy: A Dynamic Analysis
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<ART>Preference conformism: An experiment
====================================

Authors: Enrique Fatas, Shaun P. Hargreaves Heap, David Rojo Arjona
DOI: 10.1016/j.euroecorev.2018.02.009
Year: 2018  |  Pages: 71-82
ASJC codes: 2002, 2003
Keywords: Conformism, Endogenous preferences

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper reports on an experiment designed to test whether people's preferences change to become more alike. Such preference conformism would be worrying for an economics that takes individual preferences as given (‘de gustibus es non disputandum’). So the test is important. But it is also difficult. People can behave alike for many reasons and the key to the design of our test, therefore, is the control of the other possible reasons for observing apparent peer effects. We find evidence of preference conformism in the aggregate and at the individual level (where there is heterogeneity). It appears also to be more consistent with Festinger's epistemic account of why it might occur than that of Social Identity Theory.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

By suggesting in Middlemarch that people conform to the behavior of their own group so as
to be able to distinguish themselves from members of other groups, George Eliot appears to
anticipate Social Identity Theory (see Tajfel and Turner, 1979; Akerlof and Kranton,
2000). In so far as such conformism arises because people's preferences become alike, her
suggestion is also potentially troubling for economics. In welfare economics, for
instance, it is the identification of an individual with their preferences that makes the
Pareto criterion appealing. To the extent that individual preferences are endogenous and
bend to those of others in some process of preference conformism, the appeal of the Pareto
criterion is diminished. Likewise in both micro and macroeconomics, individual preferences
are often taken as the bedrock upon which economic modeling proceeds because they are
assumed not to change: ‘de gustibus non est disputandum’ (see Stigler and Becker, 1977;
Lucas, 1976).1 This paper is concerned with whether there is evidence that people exhibit
preference conformism. As Social Identity Theory attests, the possibility of motivational
conformism has long been important in the other social sciences. David Riesman's famous
book from the 1950s, The Lonely Crowd, that gained him a place on the front of Time
magazine, was based on the diagnosis that modern societies, and particularly the US, were
distinguished by the rise of a conformist attention to one's peers. In making this
argument he was developing a point first made by de Tocqueville about the US. Hannah
Arendt's equally, if not more, famous book from the 1950s, The Origins of Totalitarianism,
made conformism a part of the explanation of how ordinary people were swept along by the
rise of the Nazi party. Edward Said's celebrated late 20th century book, Orientalism,
turns in part on a similar observation to that of Elliot: that individuals identify
themselves through the contrast they find (or imagine) with those outside their group.
Whether preference conformism occurs also matters for some evolutionary accounts of group
selection. This is because, when individuals conform to the behavior of their group, the
differences in individual behavior, on which selection turns, become the same as those
that distinguish groups (see Boehm, 1999). If for these reasons, it is important to know
whether people exhibit preference conformism, it is also difficult. This is because people
behave alike for many reasons and not just because people's preferences become alike.
People often open their umbrellas when it rains – a common event triggers the similarity
in behavior without any change in preferences. It also pays to do what others do when
playing a coordination game. Equally people may extract information about the state of the
world from the actions of others in what proves to be an information cascade yielding
similarity in behavior (e.g., see Bikhchandani et al., 1992). Again, even though such
cascades can sometimes lead one astray, there is no doubt that it can be rational, in the
sense of acting upon exogenously given preferences, to be guided by others in this way.
Individuals may also act alike when they have a preference for status or social approval
that comes from behaving in accordance with a social norm (see Jones, 1984; Bernheim,
1994). A preference for following ‘the fashion’ can have the same effect, as can a social
preference like inequality aversion in some settings (see Lahno and Serra-Garcia, 2015).
The challenge in testing for preference conformism, therefore, is to disentangle these
possible ‘untroubling’ sources of similarities in individual behavior. This is often
difficult (see Angrist, 2014) and explains why we have adopted an experimental approach. A
suitably designed experiment can, in principle, control for the ‘untroubling’ causes of
conformism. If conformist behavior is still revealed, then it points to the troubling kind
of preference conformism. Our experimental design has six novel features for this purpose.
First, we focus on non-strategic decision problems to avoid the possibility that any
similarity in behavior is triggered by reciprocation.2 There are some experiments that
examine whether people follow norms in social dilemmas (e.g, see Kimbrough and
Vostroknutov 2016; Carpenter, 2004; Gachter et al, 2013). Such norm-following is
potentially relevant because it can be interpreted as social preference conformism.
However, such behavior is also consistent with a simple form of reciprocation and, to
avoid this confound, we focus on non-strategic decisions where reciprocation does not
naturally arise. The use of non-strategic decisions also helps avoid another possible
confound: the in-group bias in social preferences that has been revealed in social
dilemmas (e.g. see Chen and Li, 2009; Hargreaves Heap and Zizzo, 2009) might also produce
apparently conformist behaviors. There are some non-strategic decision experiments that
examine peer effects. Cason and Mui (1998) find that peer information has an effect in a
dictator game, but this information appears to be a prime for social preferences and not
for conformism as such. There are also experiments involving choices over independent
lotteries, where there is evidence of peer effects. That is, information about what others
have chosen (which cannot convey any information about the state of the world) appears to
influence individual lottery choices (e.g., see Cooper and Rege, 2011; Goeree and Yariv,
2015; Lahno and Serra-Garcia, 2015; Gioia, 2017).3 The peer effects are mixed in the sense
that some subjects follow and some avoid what others do. Those who follow typically
predominate (although see Corazzini and Greiner, 2007, where non-conformists predominate,
and Duffy et al., 2015, who find that, when subjects must choose private or social
information and the optimal choice varies, there is a balance between the ‘lone wolves’,
who err on the side of private, and the, ‘herders’, who err on the side of social
information). When people follow what others do in these experiments it could be because
they have a preference for sharing in misery or inequality aversion rather than because
they have some tendency to preference conformism. The evidence on this is again mixed.
While Corazzini and Greiner (2007) and Goeree and Yariv (2015) reject the inequality
aversion interpretation, Cooper and Rege (2011) find support for the sharing in misery
interpretation (what they refer to as a form of ‘social regret’ motivation) but Gioia
(2017) rejects this possibility.4 Our next feature is a response to this ambiguity over
interpretation. Second, we have a range of different types of non-strategic decision
problems. In addition to the lottery decisions discussed above, there are dictator-like
distribution decisions and choices over ordinary goods. This is new and important because
social regret or inequality aversion might apply to one type of problem, but it would not
obviously apply to all problems. Thus if we find that individuals exhibit conformism
across all types of decision problem, then, on Ockham's Razor grounds, it is more likely
that that they have a general tendency towards preference conformism rather than several
idiosyncratic preferences which explain their conformism across all types of decision
problem. Third, the decision problems are chosen so that the value of the options do not
depend in any obvious way on a state of nature that might be revealed by other people's
decisions. This avoids the possibility that behavior follows an information cascade.
Fourth, we only give individuals peer group information in the form of what someone in
their group has done in the past. This avoids peer information being developed
endogenously within the laboratory and so gives control. It also reduces the possibility
that decision-specific preferences like social regret and inequality aversion might be
triggered because the peer information refers only to ‘one person’. The peer information
is in this sense weak. The next design feature adds to the slightness of the group
information and so contributes, with this feature, to making this a ‘tough’, in Popper's
sense, test of preference conformism.5 Fifth, we assign individuals to either the ‘red
group’ or ‘blue group’ (e.g. see Hargreaves Heap and Zizzo, 2009). The groups are
artificial and this is likely to weaken any influence that they have on individual
behavior. It also means that the likelihood of subjects drawing in an habitual manner on a
desire for social approval or status from behaving in accordance with a social norm that
might come from membership of the same natural group outside the laboratory is much
weaker. There are, for instance, no ‘red group membership’ habits outside the lab that
might be drawn upon unconsciously inside. Six, individual decisions remain private. This
militates against the generation of any feelings of social approval or status within the
lab because they depend on others knowing about your actions (although you may still
derive a sense of self-image). The two group feature of our design is also noteworthy in
two respects. It allows us to test for whether any influence of peer information on
behavior in the lab arises through an experimental demand effect. We explain this in more
detail below. The feature also enables us to distinguish between two accounts of
preference conformism in psychology. In Social Identity Theory, it may seem puzzling that
individuals gain a sense of identity by acting like other members of their group, but not
when there is more than one group and groups behave differently. Individuals acquire a
distinct (social) identity through the differences in the way that groups behave. As a
result, individuals not only pay heed to what others in their group are doing, they also
take a cue on how to behave from those outside the group by avoiding in some degree what
they do (see Gino et al., 2009, for experimental support and, from popular culture, Dr
Seuss's ‘Sneetches’). Against this view, Festinger (1954) interprets the attention to what
others do differently: its origins are epistemic and come from an individual drive to
evaluate one's uncertain opinions (and abilities). We call this ‘cognitive appraisal’. It
arises when a gap between one's own tentative opinion/tastes and that of others suggests a
possible incorrectness or weakness in them which leads one to revise them in the direction
of what others value. He argues, on the basis of a variety of experiments, that the
strength of this social influence depends on the strength of a person's ties to their
group. Thus what people in another group do would be less relevant than that of one's own
group, but unlike Social Identity theory, their behavior would not be a cause for doing
different.6 In the next section, we describe the experiment in more detail and set out the
hypotheses that we test. Section 3 gives our results. We find evidence of preference
conformism in the aggregate and at an individual level (and in the latter there appears to
be heterogeneity). While a part of this may be the result of a demand effect, it cannot be
wholly attributed to such an effect; and the evidence tends to support Festinger's account
of why such conformism might occur. Section 4 discusses these results and concludes that
Mill on liberty, who also worried about the prospect of conformism (see quote above),
might be a better source, at least in welfare economics, for framing policy interventions
once preference satisfaction loses some of its attraction.

<h>EXPERIMENTAL DESIGN AND HYPOTHESES</h>
----------------------------------

Individuals came to the laboratory and were told that they would be making the same set of
decisions in two stages. Instructions about the second stage were presented only after the
conclusion of the first stage. There were 9 separate Decisions, as set out in Table 1. In
each case there are 5 options and the individual had to choose one. The first 3 Decisions
are simple choices over objects. Two of these refer to familiar objects (flowers and
drinks) and one contains unfamiliar ones, the selection of a country from countries,
mainly the eastern provinces of the old Soviet Union, ending in ‘tan’. We refer to these
as the ‘label’ decisions. The next two problems are allocation, dictator-like decisions.
With two commonly identified social preferences for efficiency and inequality aversion,
the options in Decision 5 can be ranked (efficiency is the same but the degree of
inequality changes), but the options in Decision 4 cannot be ranked in general if both
considerations are in play (because there are changes in efficiency and inequality). The
final 4 Decisions refer to risky options: they are the lottery decisions. The options in
the last two can be ranked according to their risk. In the first stage, subjects were
allocated to either a Red or a Blue group and have to choose one option in these 9
Decisions. In the second stage, subjects made the same 9 Decisions (in the same order) on
five occasions (i.e., they made choices in each Decision five times consecutively). They
also received information about what others had chosen. Treatments are distinguished
according to this information as follows. Treatment 0 (Baseline) = no peer group
information Treatment 1 = information on a person's choice from own group in the past.
Treatment 2 = information on a person's choice from the other group in the past. Treatment
3 = information on a person's choice from both groups in the past. In Treatments 1, 2 and
3, the information about own or other group choice was phrased on the screen as ‘someone
in your group chose….’. We call this the own and other peer signal and we identify a
conformist peer effect when the likelihood of an individual choosing an object is
increased by an own peer signal of that object. Treatments 1 and 3 supply own peer signals
and so provide a test for this effect. We selected two signals (one for each ‘own’ group
signal) on the basis of how people chose in each group in Treatment 0. In particular, in
the Decisions that cannot be ranked (1, 2, 3, 4, 6 and 7), we selected the two options
that were chosen with the smallest frequency. In the Decisions that can be ranked (5, 8
and 9) we selected the two with the biggest distance between them subject to the
constraint that both were selected less than 25% of the time. In other words, we aim to
have signals in the Treatments 1–3 that are rarely selected in Treatment 0 ensuring that
any resulting effect of conformism should be ‘surprising’ given the individual choices.
The two signals thus selected were randomly assigned: i.e. one to each group as their ‘own
‘signal (see note below Table 1 for details and the online Appendix for a screenshot of
how signals are presented to subjects). Treatment 0 is also important for our test for the
influence of these peer signals in Treatments 1-3 because it provides a control for any
systematic changes in decision making that arise from the mere fact of repetition and
which could give the appearance of a peer effect. Cooper and Rege (2011), for example,
find that there is a reversion to the mean in their experiment with the result that
choices naturally gravitate upon repetition towards the average of what has been observed
in the past. Hypothesis 1a follows. (peer effects): After controlling for any change due
to repetition, individuals tend to follow their own peer signal. Any such tendency in the
choices that we observe could arise either because all individuals have such a (possibly
random) tendency to follow others or because some individuals have such a tendency.
Hypothesis 1b follows. (individual consistency in peer effects): After controlling for any
change due to repetition, individuals who follow their own peer signal on one or some
Decision(s) are more likely to follow their own peer signal on the other Decisions. The
scope for subjects to make judgments regarding status and social approval seem more likely
in Decisions where the choices can be ranked because distance between options can be
meaningfully measured. Thus, in so far as we have not entirely eliminated the possible
influence of a preference for status/social approval through the private nature of the
decisions and the artificial creation of groups, we would expect if such preferences are
in play, the peer effects will be stronger in these problems. H1c follows. (social
status/approval peer effects): After controlling for any change due to repetition,
individuals are more likely to follow their own peer signal in Decisions where choices can
be ranked. If a peer influence is revealed in the test of H1, then it could arise from a
‘demand effect’: the subjects could follow the signal regarding what others do, not
because it is what others do, but in response to the fact that this is a signal from those
who have designed the experiment. To test for this possibility, we compare the ‘peer’
effect in Treatment 1 with that in Treatment 2. There is a single signal from the
experimenter in both cases and if this is all that matters, then we should expect a
similar effect on behavior. If however, it is the peer group aspect of the signal that
matters, then we expect the influence to be stronger when it comes from own group
(Treatment1) than from the other group (Treatment 2). (demand effects only): After
controlling for any change due to repetition, the peer effect is the same in Treatment 1
as in Treatment 2. The next two hypotheses concern two views on the origins of conformist
preferences and we test them using Treatment 2 and 3 where there are other group signals.
(Social Identity Theory): After controlling for any change due to repetition, individuals
tend to avoid the other group signal (i.e. choose it less frequently). (Cognitive
appraisal): After controlling for any change due to repetition, individuals tend to follow
other group signal but less frequently than their own group signal. Experiment was
conducted at the Economic Science Institute laboratory of the Chapman University. 60
subjects drawn from the general student population were randomly allocated to each one of
our four treatments (Total 240 subjects). Before each stage, subjects read the
corresponding instructions on their screen (see Appendix A). In each session, subjects are
randomly assigned to one of four orders of the Decision sequence. These were predefined
and drawn randomly at the time of the experiment (see online Appendix). Subjects were
assigned randomly to either the Red/Blue group. Within each Decision, options were
presented in a row and positions were randomized across periods and subjects. Decisions
1–3 (labels) were incentivized weakly (in a gift exchange manner) with a fixed payment of
10 ECUs. In Decisions 4 and 5 (dictator), subjects retained the number of ECUs that they
did not allocate to the other person and the ECUs they were allocated as recipient. In
Decisions 6–9 (lottery), subjects received the amount of ECUs resulting from a
computerized random draw in their chosen lottery. Every choice was paid in ECUs at the end
of the experiment. The exchange rate of dollars to ECUs was $1 = 75 ECUs. Subjects made an
average of $15 (including $7 as show up fee) for an average 40  minute experiment. This
means that the pay-off from any individual choice, while non-zero, is modest. These modest
pay-offs together with repetitions could encourage portfolio effects with individuals
spreading choices. This would produce changes between Stage 1 and 2, but there would be no
pattern of conformism in them.

<h>RESULTS</h>
-------

We first check for possible order, position and color effects. Subjects faced Decisions in
one of four different orders. A chi-square test rejects at the 5% level the null
hypothesis that the frequency of a particular option is the same across orders in only 7
out of 45 possible cases (so, the tests cannot reject the null that frequencies are the
same across the different orders in 38 out of 45 cases). Thus, there seem to be no
systematic order effects. It is possible that the position of the options has an effect
(e.g., subjects tend to choose the option on the far left). A chi-square test pooling data
across subjects and Decisions does not reject at the 5% level the null hypothesis that the
frequency of individual choices is the same across positions (p-value: 0.482).7 Thus,
there seem to be no systematic position effects. Subjects drawn from the same population
are randomly allocated to either a Red or a Blue group. For each Decision in the first
stage, a chi-square test rejects at the 5% the null hypothesis that individual choices are
the same across groups in 1 out of 9 cases (Decision 6).8 Thus, there seem to be no
systematic effects associated with Red versus Blue. Finally, there should be no difference
across treatments in terms of choices in the first stage. For each Decision, we compare
the distributions of the four treatments and a chi-square test cannot reject the null
hypothesis that choices are not different across treatments in 9 out of 9 Decisions. We
turn now to the test of our 4 hypotheses. Table 2 gives the mean number of times (out of
5) with which subjects in different Treatments follow their ‘own group signal’ and ‘the
other group signal’. In Treatment 0 subjects are not provided with this information, we
provide it here for the purposes of comparison with the other Treatments. So, for example
in Decision 3, subjects in the second stage of Treatment 0 actually choose the item that
we used as an own group signal in Treatment 1 less than would be expected by chance (and
average 0.82 times out or 5); whereas in Treatment 1 where they receive this signal they
choose the item more frequently than you would expect by chance (an average of 1.72 times
out of 5). A Mann Whitney test compares the mean frequency of ‘following own’ and
‘following other’ in stage 2 of Treatments 1–3 with the control frequencies of the choice
of these options in Treatment 0 (that is when choices occur for entirely personal
idiosyncratic or random reasons because there is no information about any other subject's
behavior). Two things are apparent in this overall summary. First, there is always a
tendency to follow ‘own signal’ in Treatment 1 (as compared with Treatment 0 choices) and
this is significant at 5% or better except for Decision 2 where it is not significant and
Decisions 1 and 6 where it is significant at only 10% level. This counts in favor of H1a.
The same tendency can be found in Treatment 3, but it is statistically weaker (we pick up
on the fact that it is weaker when discussing Result 5). Against, H1c and the influence of
status and social approval, the Decisions that can be ranked (5, 8 and 9) do not appear to
have stronger peer effects than the other Decisions in either a quantitative or
statistical significance sense. These statistical tests on the aggregate data are
potentially subject to a multiple hypothesis testing critique. As a result, we reproduce
the analysis in Table 3 at the level of type of Decision (label, dictator and lottery).
The same pattern emerges. The frequency of following ‘own signal’ is statistically
significantly higher in Treatment 1 than the choice of the same options in Treatment 0 in
each Decision type; and these differences are still statistically significant after the
conservative Bonferroni adjustment of the test statistic for multiple hypothesis testing.9
We now turn to the evidence on these points from individual random effect Poisson
regressions in Table 4. In these regressions, we consider the possible influences on the
count of an individual ‘following own’ signal and ‘following other’ signal for a given
Decision. In each case there are several specifications. They share a control for the
initial choice in stage 1 (whether it coincided with ‘own signal’ or ‘other’ signal),
dummies for each Treatment and dummies for Decision types. First, we note, in favor of H1a
that the coefficients on Treatment 1 dummy and Treatment 3 dummy (where there are own
group signals) are positive and significant in the ‘follow own’ signal equations. The
sizes of the coefficients are also interesting. It is bigger in Treatment 1 than Treatment
3, where they are respectively 70% and 50% of the size of the coefficient on initial
choice. The effect of conformity in this sense may be smaller in both cases than the
influence of consistency coming from ‘initial choice’, but, with 50–70% of the influence
of consistency, these conformity effects are quantitatively non-trivial. (Again we pick up
on the fact that the own group effect appears weaker in Treatment 3 than Treatment 1
below.) Second, there is weak evidence in favor of H1c as the dummy for the ranked
Decisions is positive and significant at a 10% level.10 (consistent with H1a): Individuals
are more likely to choose an object when they know a member of their own group has done so
in the past. (mixed in relation to H1c): There is only weak evidence in individual
regressions and none in the aggregate data that following own signal is more likely in
Decisions where the options can be ranked. Turning to H1b, we classify a subject as a
‘follower’ in a Decision in Treatment 1 if they follow their own group signal when they
did not initially choose this option, on at least half occasions that they encountered
this Decision with the signal. We now use this individual Decision determination to create
a ‘follower’ index for each type of Decision (Label, Dictator, Lottery): it is given by
the proportion of Decisions in that type of Decision that the person is classified as a
‘follower’ (e.g. for Labels, the index takes on 0, 0.33, 0.67 or 1 as there are 3
Decisions). We now test H1b by considering whether knowing this ‘follower’ index for one
type of Decision helps predict a subject's propensity to follow the own group signal in
the other types of Decision. We do this by entering the ‘follower’ index as an explanatory
variable in the regression in Table 5 on the individual frequency of following own group
signal, along the lines of the earlier individual regressions in Table 4, except we now
drop the observations from the Decisions that we have used to calculate the Follower
index. As it helps in addressing the next hypothesis, we can do the same for the subjects
in Treatment 2 to construct a ‘follower’ index of the ‘other group’ signal and we can
include them in this regression and allow for a possible difference in frequency and the
influence of the ‘follower’ index by a Treatment dummy that takes a value of 1 (0) for
Treatment 1 (2). Table 5 gives the results (column 1 tests for the influence of the Label
‘follower’ index on the other decisions, column 2 for the influence of the Dictator
‘follower’ index, etc.). The FollowerLabel, FollowerDictator and FollowerLottery by
themselves are negative but not significant. The interaction with the variable treatment
presents positive coefficients (and similar magnitude to the coefficient on the control
for Initial choice) but it is only significant for the FollowerLottery. When we test for
whether the sum of the Follower and the Follower interacted with the Treatment dummy are
significantly different from zero, we find that the p-values are 0.1778, 0.0349 and 0.0545
for FollowerLabel, FollowerDictator and FollowerLottery, respectively. This means, with
these definitions, that the extent to which a person is a ‘follower’ in Treatment 1 in
either the dictator or lottery type of Decision in Treatment 1 helps predict (positively)
their frequency of following the own group signal in the other Decisions in Treatment 1.
However, it is not helpful in predicting decisions in Lottery or Dictator decisions to
know the extent to which a subject is a ‘follower’ in Label decisions. In contrast in
Treatment 2, none of the follower indices are themselves significantly different from zero
(i.e., they only become significant when interacted with the Treatment dummy). The
assumption concerning who is a follower in the construction of our Follower index is, of
course, arbitrary and so these results are only illustrative. However we check for their
robustness in two ways. First, we select a Decision at random for each subject and apply
the same rule to classify that person as a ‘follower’ or not. In an analogous fashion, we
then examined whether this classification helped predict the frequency of following the
own group signal in the remaining 8 Decisions. The precise results depend on the original
random selection of the Decision for the classification, but we report a typical result in
the online Appendix (Table B4). The coefficient on ‘follower’ is again significant and
roughly 55% of the size of the coefficient on the influence of an initial choice of this
object. Second, we re-estimate Eq. (5) using OLS with clustered errors at the individual
level. The results are stronger in terms of the predictive power of all three Follower
variables in Treatment 1 Decisions and are reported in the online Appendix (Table B5).
(consistent with H1b): Knowing that a subject is a ‘follower’ in either dictator or
lottery Decisions in Treatment 1 helps to predict their likelihood of following their own
group signal in the other Decisions. Before we turn to the remaining hypotheses, we
explore tentatively what conformism looks like in our sample in Treatment 1 where the
evidence of following the own group signal is strongest. First, how many conformists are
there? Suppose we use our ‘follower’ classification in each Decision and adopt some
plausible cut-off number of Decisions where being a ‘follower’ makes you a ‘conformist’.
Suppose, for instance, we define a ‘conformist’, for this purpose, as someone who is a
‘follower’ on at least 4 of the Decisions.11 There were 23 who followed the own group
signal with at least this frequency, but we exclude 7 of these subjects from being
‘followers’ on our definition because they also chose their own group signal initially.
Our test does not allow us to distinguish whether their behavior reflects consistency or
‘following’. Thus there are 16 clear, with this definition, ‘conformists’ in our sample of
53 where the test can distinguish (or possibly a maximum number of 23 from the sample of
60, if we put all 7 into the sample as conformists). In other words, anything between 25%
and 40% our population could be ‘conformist’. Of course, the definition is arbitrary. But
it is not implausible and the numbers showing these ‘signs’ of conformism are non-trivial:
they are not a small fringe even if they are in a minority. Second, what are the
characteristics of the conformists? One way of answering this is to develop an analogous
definition of ‘consistent’ choice to identify people who show similar ‘signs’ but this
time of ‘consistent’ choice: in this instance, they follow their initial choice at least
twice on at least 4 Decisions. 41 of our subjects are ‘consistent’ in this sense. These
definitions of ‘conformist’ and ‘consistent’ are, of course, illustrative but they are
interesting because they allow for overlap. So, people could both show signs of
‘conformism’ and ‘consistent’ choice under them. Indeed, 12 of our 16 subjects who show
‘signs’ of ‘conformism’ also show ‘signs’ of ‘consistent’ choice. In other words, most of
the ‘conformists’ also shows signs of what from the point of economics looks likely
perfectly normal behavior. They are not otherwise erratic choosers.12 This is one way of
thinking about whether Arendt's conjecture that many, otherwise ordinary people are prone
to conformism. Alternatively, we could use our ‘follower’ indices as the measure of
conformism and see whether individual differences in the value of these indices are
related to gender or attitudes to risk and inequality. We have measures of the latter
attitudes from stage 1 choices in Decisions 4, 5, 8 and 9. None of these individual
controls was significant (see Table B7 in the online Appendix). In this sense, there is no
obvious individual characteristic associated with conformism in our sample. Our next
result concerns the relative influence of the ‘own group’ as compared to the ‘other group’
signal. We first present the supporting evidence for the substance of this result on the
relative influence and then comment on the interpretation of this evidence in relation to
H2 (i.e. the hypothesis that what we have observed in Result 1 is due to a demand effect).
In the aggregate data of Tables 2 and 3, there is evidence that individuals also follow
the other group's signal in Treatment 2 when this is the only signal: that is, the
frequency of ‘following other’ increases between Treatment 0 and Treatment 2. However,
this is a weaker effect than the one reported in support of Result 1 on the own group
signal in Treatment 1. The difference in the Treatment 2 as compared with Treatment 0 is
only statistically significant in 3 Decisions (and one at 10% levels) in Table 2 and one
type of Decision in Table 3. This compares with the much stronger evidence on following
‘own group’ signal in the aggregate data in Treatment 1, noted above. The individual
regressions in Table 4 also support this difference. The coefficient on Treatment 2 dummy
in the ‘follow other’ signal equation is positive and significant in Table 4, but it is
smaller than the analogous coefficient from Treatment 1 on the influence of the ‘own
group’ signal and this difference is statistically significant (p-values: 0.0495 in (1)
and 0.0192 in (2)). Further in Treatment 3 where the subjects receive both signals, the
coefficient on ‘follow own’ is positive and significantly different from 0; whereas the
coefficient on ‘follow other’ is not significant. Again, the ‘own group’ effect is more
powerful than the ‘other group’ signal. The final piece of evidence on the difference in
behavior in relation to own and other group signals comes from Table 5 (and is summarized
in Result 3). Following own group signal can be useful in predicting future behavior in
Treatment 1 but following the other group signal is not useful in Treatment 2. We state
that Result 4 tells against H2. This is for the following reasons. The evidence of
following the other group signal in Treatment 2 is consistent with a demand effect because
subjects could be responding to a piece of information provided by the experimenter. It is
also consistent with the Festinger's Cognitive appraisal hypothesis because, on this
account, subjects will treat other group information as potentially indicative of what to
do. Accordingly, the evidence from Treatment 2 might be thought at best to set an upper
bound for the demand effect. Consequently, if the influence of the own group signal in
Treatment 1 exceeds that of the other group signal in Treatment, the tendency to
conformism in Treatment 1 cannot be entirely explained by a putative demand effect. We
arrive at the same conclusion when we consider the evidence on individual behavior in
Treatment 3 given in Table 4. Treatment 3 is the least likely to produce a demand effect
because the experimenter here provides two opposing pieces of information. In this sense,
there is no clear lead or prompt from the experimenter through the experimental design.
If, as we find, subjects follow the own signal but not the other signal in these
circumstances, it suggests that they find the own signal more salient for reasons other
than mere experimental suggestion because this applies equally to the other group signal.
(against H2): Subjects are more likely to follow ‘own’ signals than ‘other’ group signals.
Our final result concerns the direction of the influence from the other group signal. To
summarise the evidence that has already been presented on this in support Result 4, it is
never significant and negative. It is either positive and significant in Treatment 2 or
insignificant in Treatment 3. In short, there is no evidence that subjects avoid the other
group signal (as in H3) and some evidence that they are influenced in the manner suggested
by H4. The key to the interpretation of this Result, however, in relation to H3 and H4 is
whether the positive effect of the other group signal in Treatment 2 is wholly a demand
effect. If it is not and there is some genuine following of the other group signal, then
this counts against H3 but is consistent with H4. On the other hand, if the positive
effect in Treatment 2 is entirely a demand effect, then this evidence neither tells in
favor nor against H3 and likewise H4 (because it is just a demand effect). To help resolve
this question, it is potentially helpful to look across all three treatments for a measure
of congruence between the results of each. We have already noted that the coefficient on
‘follow other’ in Treatment 2 in Table 4 is significantly smaller than that own ‘follow
own’ in Treatment 1. This difference, if we assume for this purpose that the ‘follow
other’ influence arises wholly from a demand effect, captures the genuine influence of
conformism. This suggests an influence of conformism in Treatment 1 equal to c.0.25 or
c.20% of the effect that comes from the ‘initial choice’ control. However, in Treatment 3
where demand effects are much less likely, the size of the coefficient on ‘follow own’ is
around 0.5 or 50% of the influence from the ‘initial choice’ control. This higher figure
for the genuine conformist influence of the own group in Treatment 3 suggests that the
‘follow other’ coefficient in Treatment 2 cannot be wholly a consequence of a demand
effect (i.e. we need to subtract something less than 0.5, the whole Treatment 2
coefficient, from the Treatment 1 coefficient to get a residual equal to 0.5 for the
genuine conformist effect suggested in Treatment 3). To be specific, a demand effect
equivalent to c.0.2 on the coefficient in Treatment 1 would yield a similar residual
coefficient for the genuine influence of conformism in this Treatment to that found in
Treatment 3 (i.e. 0.5). But if c.0.2 on the coefficient captures the demand effect, this
leaves 0.3 on the Treatment 2 coefficient as genuine following of this signal.13 For this
reason, we conclude that this Result, although not decisive, mildly favors H4 over H3.14
(mildly favoring H4 over H3): Subjects do not avoid other group signal.

<h>DISCUSSION AND CONCLUSION</h>
-------------------------

In what is a ‘tough’ test in Popper's sense, we find evidence of a peer effect on behavior
(Result 1). This evidence points to preference conformism because the other possible
sources of behaving alike are unlikely to be important in these decision tasks. For
example, it is difficult to be motivated by status and social approval when actions remain
private; and there is only weak evidence that these peer effects are stronger in decision
problems that can be ranked where the scope for such sentiments is stronger (Result 2). In
addition, we find that individuals’ tendencies to conformism exhibit a measure of
consistency across the Decisions (Result 3). This is important. The evidence of peer
effects could have arisen in our experiment because individuals had some random propensity
to follow the signal of what some other person was doing. Indeed, this might be the way
that an experimental demand effect would operate. However, the evidence on consistency in
conformity tells against this. So does the direct evidence on demand effects: while there
is some evidence that is consistent with a demand effect, it is patchy and even if taken
at face value, it would not account for all the conformism we observe (Result 4). Although
this is important new evidence for the existence of preference conformism, it is perhaps
not so surprising. Imitation is a well-known form of learning and in other experiments
imitation captures a relatively large fraction of behaviors (e.g. see Apesteguia et al.,
2007). Furthermore, there are evolutionary models where preferences are selected because
they have survival value: i.e. preferences are, in effect, imitated and become endogenous
(e.g. see Huck and Oechssler, 1998). Where the decision tasks that people face require
equilibrium selection or shared social preferences to achieve more efficient outcomes,
such a process of endogenous preference formation will yield in important respects shared
preferences: that is, a form of preference conformism (see Bowles and Gintis, 2011). In
turn, habits of preference imitation that have evolved to solve social dilemmas may easily
carry over to other types of decision problem. There are also two prominent theories in
psychology that predict forms of preference conformism. Our evidence mildly seems to favor
Festinger's over Social Identity theory. Preference conformism is potentially troubling
for some parts of economics and so these results are important. How troubling, of course,
depends on the extent of such conformism and the nature of the trouble caused. On the
numbers, our illustrative basis for classifying subjects as ‘conformists’ is, in this
respect, arbitrary and so our figure of anything between 25% and 40% could easily change.
Nevertheless, this way of coming up with a number and the fact that the coefficient in the
individual regressions on the own group signal is as much as 70% of the size of the
coefficient on whether someone initially revealed a preference for this object when there
was no peer information suggests that the magnitude of conformist influence is non-
trivial. What, then, is the nature of the trouble? It is not deeply worrying for positive
economics because modeling depends on some plausible foundational assumptions regarding
behavior. What is required for this is some behavioral regularities and not that they
should be derived from a model of preference satisfaction alone. In this respect the
evidence from this experiment joins the growing evidence from behavioral economics that
there are many regularities in behavior that are not (or not easily) derivable from the
preference satisfaction model; and positive economics should take this into account. The
importance of this paper in this regard is that this particular kind of non-rational
choice regularity in behavior has not hitherto featured significantly in the list of
behavioral economic insights. The trouble is possibly deeper for welfare economics,
because the appeal of the Pareto criterion depends on taking individual preferences as
given. There are alternative criteria, however. Sugden (2004) is one example of an attempt
to define an alternative metric of opportunity and connect this to the operation of
markets when preferences are not well defined. Another comes from J.S. Mill. He is, of
course, well known as an interpreter of utilitarianism and this may seem to push him in
the direction of preference satisfaction, but his most famous work, On Liberty, presents
an alternative view. In On Liberty, Mill wants to advance a constitution of liberty
because this enables individuals to acquire their own character - that is, their
individuality through the exercise of freedom of thought, discussion and ‘experiments in
living’. He did not wish here to ground policy on satisfying given preferences because
people's preferences were naturally something in the making. His policy approach, like
that of Buchanan (1986) later, is constitutional. Policy should be focused on establishing
the rules governing outcomes and not the outcomes themselves. This, then, is the other
respect in which this experiment is important. It is an encouragement to thinking more
about some of the alternatives to the Pareto criterion approach in welfare economics.
Nevertheless, even for constitutionalists like Mill, the evidence from this experiment is
still worrying. He thought, as the quote at the beginning suggests, that conformism was
the enemy of the development of individual character. One encouraging aspect of the
evidence from this experiment in this respect, however, is Result 5. It seems that there
is stronger evidence for the cognitive or epistemic source of conformism than the Social
Identity one. This helps provide a crumb of comfort for Mill in our results. He thought
that liberty would work against conformity. In so far as the exercise of liberty provides
diversity, then our results support this conclusion. When there is an ‘other group’ as
well as the ‘own group’ signal, the ‘own group’ signal effect on behavior becomes weaker.


<h>REFERENCES</h>
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<ART>Religion, discrimination and trust across three cultures
========================================================

Authors: Swee Hoon Chuah, Simon Gächter, Robert Hoffmann, Jonathan H.W. Tan
DOI: 10.1016/j.euroecorev.2016.03.008
Year: 2016  |  Pages: 280-301
ASJC codes: 2002, 2003
Keywords: Connectedness, Discrimination, Experiment, Religiosity, Trust

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<h>ABSTRACT</h>
--------

We propose that religion impacts trust and trustworthiness in ways that depend on how individuals are socially identified and connected. Religiosity and religious affiliation may serve as markers for statistical discrimination. Further, affiliation to the same religion may enhance group identity, or affiliation irrespective of creed may lend social identity, and in turn induce taste-based discrimination. Religiosity may also relate to general prejudice. We test these hypotheses across three culturally diverse countries. Participants׳ willingness to discriminate, beliefs of how trustworthy or trusting others are, as well as actual trust and trustworthiness are measured incentive compatibly. We find that interpersonal similarity in religiosity and affiliation promote trust through beliefs of reciprocity. Religious participants also believe that those belonging to some faith are trustworthier, but invest more trust only in those of the same religion—religiosity amplifies this effect. Across non-religious categories, whereas more religious participants are more willing to discriminate, less religious participants are as likely to display group biases.

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<h>INTRODUCTION</h>
------------

In this paper, we investigate the role of religion-based discrimination in trusting and in
trustworthy behaviour when interacting with people from various social groups or cultures.
Understanding the role of religion is important, because conflict between and within
different religions is rising globally (The Institute for Economics and Peace, 2014; Grim,
2014) and fast becoming a defining feature of the post-cold war world order (Huntington,
1996). A standard manifestation of this religious conflict is inter-religious strife.
Another, newer dimension involves religious radicalisation and extremism which can turn
individuals against their compatriots and moderate fellow adherents. However, despite its
ubiquity, importance and controversy, economists have only recently developed an interest
in the effects religion has on economic outcomes (Iannaccone, 1998; Guiso et al., 2006;
Tan, 2006). Religion can influence economic behaviour in at least two ways, by creating
differential social group identities (Jackson and Hunsberger, 1999) and through individual
differences in religiosity, i.e. the strength of an individual׳s religious attachment or
commitment to a particular faith commonly measured as religious belief, ritual and
experience (Tan, 2006). Identity (e.g. Akerlof and Kranton, 2000; Chen and Xin, 2009;
Currarini and Mengel, 2013) and acculturation (Guiso et al., 2003) generally affect
economic outcomes and might act as conduits for the economic influences of religion. One
economic approach to examining these effects is the experimental economics of religion, as
critically discussed by Hoffmann (2013) and Tan (2014), where the influences of religious
variables on various kinds of individual economic decision are studied systematically in
controlled settings. Previous studies demonstrated the first effect, that individuals
treat others differently in economic contexts based on same or different religious
affiliation even when other social identifiers such as nationality and ethnicity are
shared. For example, we conducted a laboratory experiment with student participants from
different cross-cutting ethnic and religious groups in Malaysia (Chuah et al., 2014).
While participants cooperated relatively more within their own ethnic groups irrespective
of religious affiliation, having the same religion as well enhanced their cooperation
further. Conversely, participants divided by different ethnic identity cooperated more
when they shared religious affiliation. A field experiment where both Indian Hindus and
Muslims in Mumbai trusted members of their own religious groups relatively more (Chuah et
al., 2013) lends further support. However, our work as well as that of other researchers
failed to demonstrate the second effect, of religiosity, directly. In two experiments
participants of higher religiosity were equally cooperative (Chuah et al., 2014) or
trusting (Tan and Vogel, 2008) than others. These results suggest that religiosity, in
reflecting an individual׳s socialisation into and internalisation of particular religious
precepts (e.g. Ryan et al., 1993) does not independently affect consequent behaviour.
However, both studies provided hints of a second avenue by which religiosity might
influence decision making as a vehicle for taste-based or statistical discrimination. One
such hint is that among the entirely Christian participant pool of Tan and Vogel (2008),
those of known higher religiosity receive greater trust from others, and especially (but
not exclusively) from those who share this trait. The second hint is that high religiosity
amplified the higher cooperation which Chuah et al.׳s (2014) multi-cultural participants
paid their religious fellows. In this paper, we propose that religious identities serve as
cues on the nature and degree of connectedness between interacting individuals, and thus
religion influences strategic behaviour, in particular trust and trustworthiness on which
we focus here. In trust games (Berg et al., 1995; Johnson and Mislin, 2011), a sender
decides how much to trust a receiver by sending an amount of money. The receiver receives
thrice the amount sent and decides how trustworthy to be in returning a proportion of it.
In equilibrium, by backward induction, assuming that receivers are rational and money-
maximising, senders anticipate nothing in return, and so send nothing. Social
connectedness is a psychological concept describing the closeness of people e.g. family or
acquaintance, friend or foe (Aron et al., 1991; Gächter et al., 2015). We call closeness
in religion-based relationships religious connectedness. Consistent with research on
social connectedness in general (Laurenceau et al., 1998), we argue that individual
religiosity operates through religious connectedness to affect trust. Religious
connectedness increases with the duration and frequency of interactions, knowledge of
others, the extent of (mutual) self-disclosure, and the number of people in the other׳s
network one is also connected to. Religious beliefs, rituals, experiences and activities
that unite or divide people facilitates this. We consider four forms of religious
identity: (1) a connection at the fundamental level of individual religiosity; (2) group
membership based on religious affiliation to the same creed; (3) religious affinity
arising from the mere affiliation to some religion, regardless of creed; and (4) religious
anonymity, where religiosity effects operate on the wider societal level of prejudice
across social identities including non-religious ones. In turn, we examine four
corresponding religious discrimination effects on trust and trustworthiness. The first is
statistical discrimination (e.g. Mueser, 1999; Anderson et al., 2006), where more
religious people are generally believed to be trustworthier and treated accordingly. The
second is that religiosity amplifies intergroup bias on the basis of religious
affiliation. Intergroup processes including taste-based outgroup discrimination or ingroup
favouritism are strengthened by an individual׳s identification with the group (Farnham et
al., 1999; Smurda et al., 2006). The third is that religiosity is used as a social
identifier of affinity which unites religious people regardless of creed. The fourth is
that religiosity is a correlate of greater general prejudice, i.e. discrimination based on
social identity differences even in non-religion categories (e.g. Hunsberger and Jackson,
2005). For this purpose, we conduct a trust game experiment where participants can incur a
financial cost in order to discriminate between co-participants of different religions and
other social identities. We extend the trust game by allowing participants to make
decisions conditional on the social identities of co-participants they might face. We then
measure participants׳ religiosity and consider their religious affiliations, their
responses to co-participants of diverse religious affiliations, and corresponding beliefs
regarding co-participants׳ actions. In particular, we study how trustworthy senders think
receivers are or how trusting receivers think senders are. We also test how much senders
invest trust or receivers reciprocate trust. Further, we analyse whether these beliefs and
actions relate to the religiosity and religious affiliation of sender and receiver. This
informs us on the relevance of statistical and taste-based motives of discrimination, and
whether religiosity per se is related to general prejudice, i.e. on the basis of even non-
religious categorisation. Our design has a number of novel features. In many previous
experiments, discrimination was observed in a particular context such as gender or
ethnicity. In contrast, we are able to measure discrimination based on different social
identifiers which vary within a multi-national participant pool. This allows us to measure
discrimination tendencies in a more general way, and to compare these across different
social identifiers. Further, we measure discrimination in participants׳ intention or
willingness to discriminate as the resources they are willing to use in order to be able
to make decisions contingent on the characteristics of their co-participants. This
provides a graduated measure of discrimination intentions, elicited in an incentive
compatible way in line with the costliness of discrimination in many real world settings
and economic models (see Mueser, 1999). We discuss the literature and motivation in
greater detail in Section 2. We outline our experiment and hypotheses in Section 3.
Results are reported in Section 4, before concluding in Section 5.

<h>RELIGIOSITY AND TRUST</h>
---------------------

Apart from its role in inter-religious conflicts across the world, high religiosity within
all creeds plays an important part in a number of pressing contemporary social debates
surrounding home-grown terrorism, abortion, contraception and gay rights. These have clear
economic consequences. For example, Indiana׳s Religious Freedom Restoration Act allows
trade to be refused on religious grounds, while provisions for religious exemptions from
public immunisation programmes (in force in 48 U.S. states) can generate negative
externalities on an epidemic scale. This provides economists with a clear motivation to
examine the effects of religiosity in economic settings using economic methods. A few
experimental economics studies have examined the effects of religiosity (a.k.a.
religiousness, which measures an individual׳s attachment or commitment to a particular
faith) on economic behaviour. Most use religious service attendance measures as a proxy
and relate this to prosocial behaviour in experimental games.1 Generally, previous
research has found little evidence for the relationship between religiosity variables and
behaviour in the trust game. Fehr et al. (2002) found no effect of the church attendance
of German household survey respondents on their decisions in a trust game. Karlan (2005)
measured religiosity in terms of months since last religious service attendance and
related this variable to public good contributions and trust game decisions in a field
experiment in rural Peru. It was inversely related to public good contribution but only at
the 10% level of significance. Attendance also did not explain trust game decisions in
this study directly. However, participants with less frequent attendance were sent greater
amounts for unexplained reasons. Anderson and Mellor (2009) measured the frequency of
religious service attendance to serve as a proxy for religiosity. This variable was not
significantly related to public good game contributions of older adult U.S. participants.
Anderson et al. (2010) subsequently found a positive effect with college student
participants, but only when comparing the corner cases of high and low attendance. Trust
game behaviour here was unrelated to the attendance measure. Tan (2014) argued that one
reason for the mixed results in terms of effect significance and direction could lie in
the multi-dimensional nature of religiosity that simpler measures do not capture, e.g.
based on attendance alone. Unidimensional religiosity measures like these are
unsatisfactory as they fail to tap into the different motivations behind and expressions
of religious attachment (Spilka et al., 2003, p. 28; Hill and Hood, 1999, p. 5), which can
manifest behaviourally in opposite directions (e.g. Tan, 2006). For example, intrinsic
spiritual or quest motives for religious attachment are sharply differentiated from
extrinsic ones such as seeking social group identification. In response psychologists of
religion have developed a now widely accepted approach (DeJong et al., 1976) which
measures individual religiosity in terms of five dimensions, religious knowledge, practice
of religious activities, belief in religious precepts, personal mystical experience and
consequences of religion on behaviour (Glock and Stark, 1965). We used such multi-
dimensional religiosity measures in a number of previous experimental economics studies
with promising but still inconclusive results. Tan (2006) found the different components
of a multi-dimensional measure to significantly affect dictator game offers or ultimatum
game responses but in opposite directions. Chuah et al. (2009) used principal components
analysis to derive a multi-dimensional religiosity scale using 15 items from the World
Values Survey (see Inglehart, 1997) which was negatively and (marginally) significantly
associated with ultimatum game offer sizes among Malaysian and UK participants. In the
study by Tan and Vogel (2008) on German University students, higher religiosity receivers
were trusted more especially by fellow high-religiosity senders. Receivers of higher
religiosity returned greater amounts and especially to more religious senders. The results
of Tan and Vogel (2008) suggest that religiosity can have an indirect effect as a social
identity that generates ingroup favouritism. However, this is inconclusive in that
religiosity differences in this study did not explain why senders trusted more religious
receivers more. Alternatively the result could evidence statistical discrimination towards
highly religious people to the extent that they are generally held to be trustworthier.
Finally, in Chuah et al.׳s (2014) prisoner׳s dilemma experiment, shared religious creed
raised cooperation within a multi-cultural Malaysian student participant pool. In
contrast, multi-dimensional religiosity as an independent variable in its own right did
not explain cooperation. However, religiosity raised cooperation further when interacted
with the shared creed dummy variable. This result suggests a further, again indirect
effect of religiosity as an enhancer of ingroup bias based on shared religious
affiliation. Alternatively, the result could reflect the greater general tendency of
religious individuals to discriminate on the basis of different social identities
including religious creed. Let us now consolidate these results as behavioural patterns
from the perspective of religious connectedness, as outlined in the Introduction. First,
individual religiosity can increase connectedness in three ways. First, the participation
in ritual increases the duration and frequency of interactions between individuals.
Second, increases in religious knowledge and indoctrination increase knowledge of others
in the group, e.g. how they think they ought to behave (Tan, 2006). The latter relates to
the access to relevant social category, and in turn the likelihood of using that social
categories as stereotypes to guide behaviour such as trust (Tan and Vogel, 2008). Thirdly
and indirectly, common beliefs and experiences engender familiarity and closeness, which
then carry over to group identification and biases at the levels of similarity in
religiosity (Tan and Vogel, 2008) or religious affiliation (Chuah et al., 2014). Such
effects should weaken as religious connectedness weakens, via the above processes as well
as a decreasing overlap in social networks. In the limit, we have interactions across
group markers that are orthogonal to religion. If so, would individual religiosity lose
its bite on discrimination?

<hs>  Measuring trust and religion</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Following previous studies we used a trust game as a behavioural measure allowing for the
expression of discrimination (e.g. Fershtman and Gneezy, 2001; Holm and Danielson, 2005;
Falk and Zehnder, 2013). As shown in Fig. 1, we used a binary version of the trust game
because it is cognitively less demanding on participants, so as to reduce biases from
fatigue in view of the 88 games each participant had to play. The sender and the receiver
begin each game with 200 points. We test two parameterisations of the trust game. In the
first, namely the “low stake game”, the sender decides whether or not to trust, i.e. to
send 50 or 0 to the receiver. If the sender sends the money, the receiver receives three
times this amount and decides whether or not to be trustworthy by returning 100 or 0. In
the second, i.e. the “high stake game”, we increase the stakes by allowing the sender to
send 150 or 0 to the receiver, and the receiver decides whether or not to return 300 or 0.
Assuming that players are rational and money maximising, in equilibrium nobody sends any
money. By backward induction, receivers will prefer more money to less and not return
anything to the sender, i.e. not reciprocate. The sender anticipates this and prefers not
to send anything to the receiver, i.e. not trust, because the payoff from withholding is
higher than sending and not receiving anything in return. The subgame perfect equilibrium
is that neither sender nor receiver sends any money. This forms the benchmark relative to
which we can measure the trust and trustworthiness of senders and receivers, respectively.
It follows that there is low (high) temptation for the receiver to send 0, and this
implies a low (high) stake for the sender in trusting the receiver. The two games allow us
to test our hypotheses within a wider domain of stakes. In order to obtain measures of
discrimination, we administered the trust game under different social identity conditions
using the strategy method (Selten, 1967). To keep sender and receiver tasks symmetric, in
the experiment we allowed receivers to choose “return” or “not return” under the
understanding that the decision only applies if the sender had chosen “send”. In practice,
the sender׳s decision would not influence payoffs in the game if the sender does not send
any money. To make this explicit, we displayed games on the screen as extensive form
representations consistent with this strategy method setup (see Fig. 2). In the first two
rounds of the experiment, all senders and receivers stated their decision of whether to
send or not to send without knowing the social identities of their co-participants. One
round was for the high stake condition and the other the low stake condition, in
counterbalanced orders across participants. We call these actions default actions. In the
other rounds that followed, participants stated their decision based on every possible co-
participant׳s social identity type according to different social categories (see Table 1).
There were 88 rounds in total. Using religious affiliation as an example of a category,
every participant was asked whether they would send or not send to co-participants of
every religious affiliation (type) we provided, i.e. Buddhist, Christian, Hindu, Jewish,
Muslim, other or none. This process was repeated for every type of every category,
presented in random order after the tasks without social identity were performed. We call
these actions conditional actions. Each category thus constitutes an experimental
condition. In each round where participants could base their decisions on the co-
participants׳ social identities, they were provided with an additional endowment of 100
points from which they could spend an amount of their choice to increase the probability
of implementing their conditional action instead of their default action. Each point
increases the probability by 1%, and each point unspent accrues as experimental payoffs.
This incentive compatibly elicits their willingness to discriminate (WTD). When
calculating experimental earnings, we applied the participant׳s stated WTD for the
condition in concern to set the probability that the conditional action rather than the
default action was to be used, and randomly determined subject to this probability. As an
example, consider a high stake game where a participant chooses to send 150 to co-
participants of high religiosity, and 0 to other types of co-participants. Assume also
that the default is to send 0. A WTD of 20 points means that if the participant is
subsequently randomly matched with a high religiosity co-participant for the purpose of
calculating experimental earnings, there is a 20% probability that the choice of sending
150 is implemented, and a complementary probability of 80% that the default action of
sending 0 will be implemented. A WTD of 100 points means sending 150 to the high
religiosity co-participant for sure, and sending 0 to a medium or low religiosity co-
participant for sure. Higher WTD values increase the probability that discriminating
decisions are used to determine earnings and therefore represent the decision maker׳s
willingness to pay for social identity information to afford discriminating actions. This
method of eliciting WTD is novel and has two advantages. First, it experimentally models
the costliness involved in discrimination activities, e.g. it takes time and effort to
find out another person׳s religiousness or political inclination. This introduces an
externally valid dimension to the test. In retrospect, observed decisions in previous
experiments without this feature, e.g. Tan and Vogel (2008), capture behaviour “as if” the
participant confidently assumes or knows the co-participant׳s social type. Second, the
costliness of discrimination is in a way a disincentive to discriminate that mitigates
demand effects in terms of discriminating actions, and in doing so incentive compatibly
reveals the demand of the individual who despite of this cost goes for it. That said, we
should not and do not try to remove all demand effects from the experiment, for we are
interested in those germane to the act of discriminating on the basis of social
identity—to which we can clearly attribute as the cause of action. Fig. 2 shows the
experimental interface employed to elicit decisions. The interface shown in this example
is asking participant 39, assigned to the sender role (Person A) to make decisions in the
religiosity category for a low stake game (Round 4). The game tree displays the actions
and associated payoffs for participants in both roles. The dark shaded button indicates
the benchmark decision this participant has already indicated previously, which cannot be
changed (SEND). The participant must make trust decisions in the religiosity category by
clicking on either the SEND or NOT SEND buttons for each possible co-participant
religiosity type, namely “High”, “Medium” and “Low” religiosity. The participant then
indicates what proportion of the 100 points to allocate towards implementing the relevant
conditional choice, i.e. their stated WTD. Once all these decisions have been made, the
participant clicks on CONFIRM to enter them and proceed to the next round, which involves
a different category. We administered a pen-and-paper questionnaire after the completion
of the trust game task to collect additional measures. Beliefs were elicited as
participants׳ expectations of co-participant actions in the trust game. Participants were
asked (in their roles and for every possible value in every social identity category) to
state the probability that such a type of co-participant would choose to send.
Participants were paid depending on how close these beliefs were to true distribution of
choices observed in the experiment, and payments were computed according to the quadratic
scoring rule (Selten, 1998). We also recorded each participant׳s own demographic
characteristics for each of the social identity categories in order to classify them in
terms of the values for each category shown in Table 1. Notably, we elicited individual
religiosity according to the Glock and Stark (1965) dimensions using the denomination-
robust 8-item instrument by Rohrbaugh and Jessor (1975) which yields our religiosity
measure. It takes into consideration different dimensions of religion, namely belief,
ritual, consequences, theology, and experience. It delivers an individual׳s overall score
between 0 and 32 (see Hill and Hood , 1999).

<hs>  Hypotheses</hs>
  ~~~~~~~~~~

Piecing together the mosaic of results given by the literature from the perspective of
religious identity and connectedness, we shall use our experiment to test the following
four hypotheses. These explanations of behaviour are not mutually exclusive and could
operate in concert, potentially coexisting or reinforcing each other. We cater for these
possibilities in the analysis.Statistical discrimination Statistical discrimination
Senders generally believe that receivers of higher religiosity are trustworthier, and
statistically discriminate by being more likely to trust them more than receivers of no or
lower religiosity. The first possibility for the expression of religiosity in terms of
economic behaviour is statistical discrimination (e.g. Anderson et al., 2006) when a
person׳s social identity contains information regarding particular behaviour tendencies
that can feed into strategic considerations, e.g. beliefs of trustworthiness. Statistical
discrimination in the trust game applies only to senders, as they must anticipate the
likelihood that receivers will fulfil or abuse their trust if invested. Tenets such as
charity, neighbourly love and the Golden Rule are common to all religions and may confer a
trustworthy reputation on religious people (e.g. Spilka et al., 2003, p. 172). If
statistical discrimination based on religiosity is present in the current experiment, all
senders regardless of their own religiosity should be more likely to behave trustingly
towards receivers of greater religiosity levels. Senders would therefore be more likely to
send to receivers of higher religiosity, compared to receivers of lower religiosity, and
this effect should increase with the sender׳s religiosity.Ingroup love Ingroup love
Religiously affiliated senders are more likely to invest trust in receivers who are
affiliated to the same religion, relative to receivers who are not religiously affiliated
or affiliated to a different religion. This effect increases with the sender׳s
religiosity. Religiosity is a fundamental measure of religiousness as an individual. It
might vary across religious affiliations. In turn, it weakens connectedness, e.g. from
variances in religious doctrine and prescriptions for behaviour. Further, it is arguably
more subtle than religious affiliation, which may serve mainly as a badge of membership.
It follows that while religiosity might be a weaker marker of religious connectedness, it
could serve to amplify discrimination effects based on religious affiliation, which
increases the salience of religious categories as social markers. Thus, the degree to
which people exhibit biased intergroup behaviour is related to the strength of their
identification with the group concerned, and in turn increases cooperation through
stronger social preferences (Farnham et al., 1999; Chen and Xin, 2009). In particular,
greater discrimination can result from a loss in (implicit) self-esteem in people who
highly identify with a particular social group that is undergoing a threat, i.e. a
perceived negative evaluation by others (Smurda et al., 2006). In the current context this
hypothesis suggests that greater trust in co-participants of the same religious group is
relatively stronger in more religious participants in either role. Such effects are
reinforced by individual religiosity, which embodies closeness nurtured through joint
participation in activities. This, in turn, increases trust by increasing religious
connectedness through commitment to the creed, i.e. ingroup membership. Religiously
affiliated senders would therefore be more likely to send to receivers belonging to the
same creed, compared to receivers who are atheists of followers of other creeds, and this
effect should increase with the sender׳s religiosity.Religious affinity Religious affinity
Religiously affiliated senders are more likely to invest trust in receivers who are
affiliated to some—regardless of which—religion. This effect increases with the sender׳s
religiosity. The third possibility we test is that people consider their religious
affiliation or religiosity a pertinent social identity and exhibit biased intergroup
behaviour (i.e. ingroup favouritism or outgroup prejudice) towards others depending on
whether or not they are also religiously affiliated to some creed—irrespective of whether
or not it is the same one. For example, former Prime Minister of the United Kingdom Tony
Blair articulated this thinking publicly at the Westminster Faith Debate on “Religion in
Public Life” held in London on 24 July 2012,2 “I find a connection with people who are of
faith, even though they׳re of a different faith to my own, precisely because there is a
certain space, philosophically and emotionally, you can congregate around”. Put
differently, this weakens the religious connectedness relative to that between individuals
of the same creed. That said, religious affinity does not extend to group membership, and
its effect should be relatively weaker. A religious affiliate would thus be more likely to
send in the trust game to another who is affiliated to some religion—regardless of whether
or not it is the same creed, and this effect should increase with the sender׳s
religiosity.General prejudice General prejudice Religious senders are generally more
biased, such that they are more likely to send to receivers with the same non-religious
social identity. Finally, since the middle of the last century (Adorno et al., 1950;
Allport, 1954), psychological studies have repeatedly identified links between individual
religiousness and attitudes of prejudice. Such prejudice is counter to religious teachings
of charity, forgiveness, love and compassion. This link is complex and dependent on a
number of other factors including religious orientation, social desirability and doctrinal
attitudes towards particular out-groups (Spilka et al., 2003, Chapter 14). Links between
religiosity and prejudicial attitudes have been demonstrated repeatedly (Allport and Ross,
1967; Altemeyer and Hunsberger, 1992; Hunsberger and Jackson, 2005; Hunsberger, 1996;
Jackson and Hunsberger, 1999). We consider the possibility that religious people are
generally more disriminating in the context with the weakest religious connectedness. If
this holds, we should find that senders of higher religiosity have greater WTD across all
social identity categories or overall. We should also find that religious senders are more
likely to send to the “ingroup” based even on non-religious categories. In experimental
terms, we are thus testing for the effect of religion on the individual׳s inherent
disposition to discriminate.

<hs>  Procedure</hs>
  ~~~~~~~~~

We ran the experiment at the China, Malaysia, and UK campuses of the University of
Nottingham. All campuses use English as the medium of instruction, and share common degree
structures and syllabi. This participant pool affords high direct comparability of data
collected from these diverse cultures. The cultural diversity of our sample widens the
study׳s domain of validity. Such diversity increases the number of subjects of each social
identity type. Thus, there is a much larger number of ingroup and outgroup combinations,
which we shall also use to test for the cultural sensitivity or robustness of our
findings. We used a computerised interface in English with 545 student volunteers (273
senders and 272 receivers) recruited by poster and e-mail announcements for 90-min
sessions of 20–40 participants. The experimental software was programmed in Visual Basic
6, and the computerised text was in English. Our experiment followed the standards of
cross-cultural experimental economics (Roth et al., 1991; Herrmann et al., 2008).
Instructions, comprehension quiz questions, belief elicitation and demographic
questionnaire were provided in the respective local languages. The English version was
always available to participants in China and Malaysia on demand. The original English
version was first translated to Chinese and Malay, and then back translated to English to
check for consistency. Any inconsistencies were resolved in consensus with the co-authors
on this project. Translations were performed by three people who are not co-authors on the
project, but are native speakers of Chinese or Bahasa Melayu and English. All of them have
professionally worked in the respective two languages. The English version of the
experimental instructions is found in the online appendix. Participants were randomly
assigned to either the sender or receiver role throughout the experiment, and made trust
game decisions first for socially unidentified co-participants and then for each of the
social identity categories and types as described (see Table 1), for both the low and high
stake conditions, in individualised random order. After all experimental sessions were
completed, participants were randomly matched experiment-wide across the three locations,
and one social identity category was selected randomly to determine earnings. The
participants׳ total earnings were the points from the game, those remaining from the WTD
endowment, and payments depending on the accuracy of their beliefs in one randomly chosen
belief task, with the answer compared to the statistical return rate of the sample for the
type of participant. We paid participants at the rates of Renminbi (RMB) 0.20, Ringgit
Malaysia (RM) 0.08 and Pounds Sterling (£) 0.04 per point earned plus a show-up fee (RMB
25, RM 10 or £5, respectively). Earnings were collected a week after the final session to
allow for experiment-wide participant matching over the three locations. We paid
participants in the three locations RMB 63.68, RM 28.66 and £14.65 on average. Each
session lasted approximately 1.5 h. The exchange rate between the three currencies we used
was determined using the Big Mac Index published annually by The Economist magazine.

<h>RESULTS</h>
-------

Before testing our four hypotheses we look at some basic features of the data. Table A1
provides the distributions of participant types of each category across the three
locations, and a summary of mean WTD, beliefs and actions across conditions and types by
roles and locations. Religiosity scores ranged from 0 to 30 and the average was 11.9. The
mean age was 20.5 (standard deviation of 1.74). There are more females (122) than males
(65) in the Malaysian sample, more males (137) than females (27) in the Chinese sample,
and almost as many females (96) and males (98) in the UK sample. In ethnic and religious
terms, China is most homogeneous with 162 ethnic Chinese, 134 atheists and 25 Buddhists,
out of 164 participants in total. Malaysia and UK are relatively heterogeneous, with
Chinese (106) and White (115) as majority ethnicities, and Buddhists (61) and Christians
(56) as majority religions, out of 187 and 194 participants in total, respectively. In
Malaysia and UK, the non-majority religions are all represented, apart from no Jewish
participant in the Malaysia subsample. In the high (low) stake baseline games where
decisions could not be conditioned on the social identity of co-participants, 38.1%
(56.0%) of senders chose to trust, and 27.9% (43.0%) of receivers chose to reciprocate.
Further details may be found in Table A1.

<hs>  Preliminaries</hs>
  ~~~~~~~~~~~~~

We first check for independent effects of religiosity on trust, to confirm the result from
previous studies that forms our departure point. Our measure of religiosity is RELI, which
is the mean centred to avoid multi-collinearity in our regressions below, following
Marquardt (1980). There is no significant difference in the religiosity of senders who
trust and those who do not in both the high (t-test, p=0.780, 2-tailed henceforth) and in
the low stake condition (p=0.758), or for receivers in either the high (p=0.775) or the
low condition (p=0.886). To corroborate, individual level random effects binary logit
regressions controlling for beliefs, stake and gender show that religiosity does not
significantly influence trust and trustworthiness (p=0.921 and p=0.375, respectively; see
Table A1 for details). As there is no evidence for an independent influence of religiosity
on trust and trustworthiness. Senders spent an average of 21.4 and receivers 22.0 out of a
hundred points to increase the probability of implementing their conditional actions (i.e.
WTD) in the religious affiliation condition, where actions could be conditioned on the co-
participant׳s religious denomination. WTD rises with one׳s religiosity level at 19.3,
21.2, and 30.9 for low, medium and high religiosity, respectively. Senders spent an
average of 20.9 and receivers 20.0 points on WTD in the religiosity condition, where
actions could be conditioned on the co-participants level of religiousness. WTD rises with
one׳s religiosity level at 19.8, 19.9 and 26.0 for low, medium and high religiosity,
respectively. The same pattern holds for receivers at 19.5, 23.0, and 29.6 (18.7, 21.8,
and 21.5), respectively, for low, medium, and high religiosity. Further, 58.6% (50.7%) of
senders and 48.2% (43.9%) of receivers discriminate on the basis of religious affiliation
(religiosity) in the sense that they choose different conditional actions for different
types of co-participants.3 With information of religious affiliation (religiosity), 23%
(22.7%) of behaviour differs from that in the baseline: 9.2% (10.1%) increase and 13.8%
(12.7%) decrease trust. As described in Section 3.2, this widely observed discrimination
can take a number of forms as expressed in our four hypotheses, which we test next. To
control for and to test the interplay of effects from multiple variables and their
interactions, we use multivariate analysis. In the following subsections, our regressions
include individual-level random effects to control for the potential non-independence of
multiple observations per individual. We never provided participants with feedback between
choices so there is independence between observations across participants. We always
control for low and high stake conditions (STAKE=1 for the high stake condition and =0 for
the low stake condition), and for own gender (FEMALE=1 for females and =0 for males) due
to known gender effects on trust game behaviour (Croson and Buchan, 1999).4 Our
regressions always include individual religiosity RELI. Results are robust to the
inclusion of WTD or dummy variables for location (these alternative models are reported in
online appendix OA3).

<hs>  Statistical discrimination</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~

Statistical discrimination implies that senders believe that some types of receivers are
trustworthier than others. These stated beliefs are given by the dependent variable
BELIEF=0 to 1. According to Hypothesis 1, a sender, irrespective of her own social
identity, uses the receiver׳s religiosity to form an expectation of their trustworthiness.
Participants should therefore be willing to pay more than in identity conditions unrelated
to any possible statistical discrimination. Our control condition is a “birthday” category
where actions were conditioned on whether the co-participant was born on an even or odd
day of the month. There, mean WTD is 17.7 and its confidence interval is 16.1–19.2. The
mean WTDs of the religious affiliation and religiosity categories are 21.4 and 20.9,
respectively, i.e. outside the interval. We also examine how beliefs regarding the
trustworthiness of receivers vary with the decision maker׳s religiosity using a
religiosity level variable RLEV. This variable was used in the experiment to elicit
participants׳ beliefs and actions contingent on the co-participant׳s low (RLEV=0 if
religiosity questionnaire score is 0–10), medium (RLEV=1 if score is 11–20) and high
(RLEV=2 if score is above 20) religiosity.5 We test this effect on senders across all
religious affiliations. Further, to test if being of a similar religiosity level
reinforces statistical discrimination, we interact RLEV with RELI. Senders׳ beliefs that
low, medium, and high religiosity receivers would act trustworthily are 0.33, 0.41 and
0.43, respectively, pooled over both stake conditions. Average beliefs and actions are
shown broken down by participants׳ own religiosity levels in Fig. 3. Senders of diverse
religiosities believe that receivers of higher religiosity are more likely to return (top
left figure), and are more likely to send to them (top right figure). Receivers of diverse
religiosities believe that senders of higher religiosity are more likely to trust (bottom
left figure), and are as likely to return to senders of different religiosity levels.
Regression analysis (Table 2) confirms that more religious people are trusted more by
people across different levels of religiosity, as the RLEV coefficient is positive and
significant in models 1–3. This result holds overall, for people without or with religious
affiliation, as demonstrated by the regressions on the pooled sample (model 1) and
subsamples disaggregated by people without (model 2) or with (model 3) religious
affiliation. Further, the statistically insignificant RLEV×RELI coefficient in model 4
shows that senders of different levels of religiosity are as likely to believe that
receivers of high religiosity are trustworthier, confirming that statistical
discrimination holds across senders irrespective of religiosity. Statistical
discrimination Senders of all levels of religiosity believe that receivers of higher
religiosity are trustworthier, and behave consistently with this belief by trusting them
more.

<hs>  Ingroup love</hs>
  ~~~~~~~~~~~~

According to Hypothesis 2, higher religiosity strengthens the identification of
participants with the religious group they are affiliated to, and thereby amplifies
ingroup biases based on affiliation. We use WSEND as the dependent variable. To test for
ingroup biases, we define a dummy variable INGROUP that takes on the value of 1 when
participants are making decisions conditional on participants that are of the same type as
those for the category in concern. In this case of ingroup biases in religious
affiliation, INGROUP=1 when co-participants are of the same religious affiliation, and =0
otherwise. When people have information about others, they use it to guide their actions.
In turn, this feeds into behaviour. Thus, our models of WSEND include BELIEF to control
for statistical discrimination. However, beliefs do not necessarily explain behaviour
completely, for taste-based discrimination can also play a role.8 Thus, by controlling for
the effect of statistical discrimination with BELIEF, INGROUP is a measure for taste-based
discrimination, such that remaining ingroup effects are attributable to it. We include the
mean centred measure of individual religiosity RELI as well as the interaction term
INGROUP×RELI, which tests if ingroup biases are strengthened by the decision maker׳s
religiosity. Tests are performed on data from the religious affiliation condition rather
than the religiosity condition where there is no clear sense of group membership. Note
that participants were not told their own religiosity level according to our survey
measure nor asked to state their perception of their own religiosity in absolute terms or
relative to other participants. Fig. 4 shows the percentage change in trust actions in
WSEND conditional on the receiver׳s religious affiliation, relative to the baseline where
decisions are made unconditionally. In UK and Malaysia, where most participants have
religious affiliations, we observe increases in trust for the ingroup relative to the
baseline, i.e. ingroup favouritism. In China, where most participants are atheists, we
observe decreases in trust for the outgroup relative to the baseline, i.e. outgroup
prejudice. We scrutinise this econometrically. Referring to Table 3, model 7 shows that
senders are more trusting towards those of the same religious affiliation (INGROUP is
positive and significant) and this effect increases with one׳s religiosity (INGROUP×RELI
is positive and marginally significant). The figure in Table A3 shows that ingroups are
consistently trusted more than outgroups by people across different religions. This
finding is also robust to contextual differences across groups and societies.9 This
ingroup effect does not hold for atheists but for religious affiliates (see models 8 and
9, respectively). We run the same tests on receivers and find only a marginally
significant positive INGROUP effect on WRETURN of the pooled data (see model 10), which
corroborates the taste-based discrimination interpretation. Thus, we find support for
Hypothesis 2.10 Ingroup love Religiosity enhances the ingroup favouritism shown by senders
towards receivers of the same religious affiliation. This effect is driven by people with
religious affiliations. Instead, atheists discriminate on ethnicity, which can be proxied
by religious affiliation. Evidence of ingroup favouritism by receivers is marginally
significant.

<hs>  Religious affinity</hs>
  ~~~~~~~~~~~~~~~~~~

Hypothesis 3 posits that religious affiliation or religiosity can serve as social
identities irrespective of creed. Result 1 suggests this, but a stricter test involves
data from the religious affiliation condition where there is a clear demarcation of social
identity for self and other. This test distinguishes itself from previous ones in that it
considers the possibility that people trust each other more so long as they both have some
religious affiliation, even if they are of different religious denominations. Fig. 5 plots
the linear fit of sender׳s beliefs in the trustworthiness of the receiver as a function of
the sender׳s religiosity in the absence (left) or the presence (right) of religious
affinity, and hints at an effect of religious affinity, which we properly test with a
multivariate analysis. To test this formally, we derive the dummy variable AFFILIATE,
which takes on a value of 1 when a participant who is religiously affiliated faces a task
where the other is also religiously affiliated, regardless of creed. It takes on a value
of zero when either the participant is an atheist or the task involves trusting an
atheist. Referring to Table 4, AFFILIATE is positive and significant in model 11, showing
us that religious people believe that other religious people are trustworthier than
atheists. However, it is insignificant in model 12, showing us that despite this belief
they are not trusted more. Model 13 includes an AFFILIATE×RELI variable and finds that
such beliefs are amplified by the sender׳s religiosity. Model 16 corroborates model 12 and
further shows that there is no higher order effect on actions. The effect of religious
affinity on actions is weaker than that of being affiliated to the same denomination: in
models 12 and 16, INGROUP and INGROUP×RELI are positive and significant, while AFFILIATE
and AFFILIATE×RELI are not. This supports the arguments presented in Hypotheses 2 and 3
that connectedness enhances group identification. Beliefs only partially drive behaviour
on the basis of mere religious affinity. Beyond statistical discrimination driven by
beliefs, taste-based discrimination holds only if people are affiliated to the same
denomination—not just by mere religious affinity. We further scrutinise the negative and
significant INGROUP effect and its interaction term in model 13, which implies that
religiosity diminishes the belief effect for those from the same denomination. This
peculiar result of lower beliefs of trustworthiness in the ingroup is driven by atheists,
as shown by our regressions on data disaggregated by atheists and religious affiliates
(models 14 and 15, respectively). It suggests that atheists are more suspicious of each
other, even though it does not lead to lower trust. In contrast, religious affiliates
ultimately trust the ingroup more. These behaviours suggest taste-based
discrimination.Religious affinity Religious affinity Senders׳ religiosity enhances beliefs
about religiously affiliated receivers׳ trustworthiness regardless of whether or not they
belong to the same denomination, but they do not invest more trust despite this belief.

<hs>  General prejudice</hs>
  ~~~~~~~~~~~~~~~~~

Hypothesis 4 posits that more religious people discriminate more over a range of social
identities including non-religious ones. Our univariate tests examine whether more
religious participants have relatively higher WTD across the different social identity
categories we use. We construct, for each participant, an average WTD as the unweighted
mean WTD across all of them. The correlation between average WTD and religiosity is
positive and significant across both roles (ρ=0.087, p=0.0449). This relationship is
significant for senders (ρ=0.123, p=0.0442) but insignificant for receivers (ρ=0.045,
p=0.4658). Further, the average religiosity of those whose WTD is zero throughout the
experiment (μ=33.5, n=73) is significantly less than that of others (μ=40.5, n=457,
p=0.01). We also examine the correlation between religiosity and WTD across social
categories (see Table 5). Again, these correlations are generally insignificant for
receivers. For senders, information on religious affiliation, religiosity and ethnicity
are salient and serve as social identifiers that markedly separate participants. In turn,
the correlations of religiosity and the WTD along these dimensions are robustly
significant. Referring to Table 6, model 17 shows that WTD is positively related to
religiosity, which suggests that more religious people are more prone to religious-based
discrimination. Further, we test if religious participants are generally more prone to
ingroup favouritism, i.e. even if social identities of co-participants are unrelated to
religion. Fig. 6 shows that both religious affiliates and atheists generally favour the
ingroup over the outgroup by trusting the ingroup more across different categories of
social identity. Models 17–19 test WTD and ingroup biases on data concerning all non-
religion conditions. As found above, WTDs increase with religiosity (model 17). This
effect is marginally significant. For beliefs (model 18), we find a positive and
significant INGROUP effect for senders overall, but no RELI interaction effect. For
actions (model 19), we also find a positive and significant INGROUP effect for senders
overall, but no RELI interaction effect. This result is robust to controls for respective
conditions.13 General prejudice Religiosity is positively associated with the general
willingness of senders to discriminate across a range of non-religious social identities.
However, participants of different religiosity are as prone to ingroup favouritism.

<h>DISCUSSION</h>
----------

Inter-religious interaction is an increasingly important social phenomenon. However,
previous experimental work has yet to establish univocal evidence regarding its direct,
independent effects on trust and trustworthiness. To better understand this issue we
conducted a trust game experiment across three countries with participants of different
religious denominations and levels of religiosity. Our experiment was designed to test
four hypotheses for indirect effects of religiosity we derived from these previous
studies. Taken together these hypotheses propose that religiosity affects economic
behaviour indirectly by moderating (a) the way we treat others of the same and different
social groups and (b) the expectations and behaviour those we interact with develop
towards us. Our main findings can be summarised as follows. First, religiosity is a strong
social identifier which is used as a basis of statistical discrimination by senders of
varying religiosities (Result 1). Both religious and non-religious people believe that
more religious others are more trustworthy. Second, we found that religiosity enhances the
ingroup favouritism people show to others who share the same faith (Result 2). Senders of
all religions believe receivers of the same faith to be more trustworthy and follow these
beliefs with actions in step with their own degree of religiosity. Third, we found a
religious fellow feeling or affinity between religious people across different faiths,
i.e. irrespective of whether they share the same one or not (Result 3). This was expressed
in the greater belief people with religious affiliation have in the trustworthiness of
others similarly affiliated. As before, individual religiosity amplifies this effect. This
kind of religious affinity, however, does not generate quite the same positive effect on
actual behaviour. Fourth, while we found that religiosity is associated with a willingness
to discriminate across non-religious categories, observed ingroup favouritism did not vary
with religiosity (Result 4). Since the 1950s, Adorno et al. (1950) and Allport (1954) have
postulated general religious prejudice, but have since been met with scant reliable
evidence. In summary, we uncovered evidence that religion operates indirectly through
social identities and religious affiliation, which are used as a basis for discrimination
in trust games. Religious identity is one dimension that tells decision makers how they
are connected to those with whom they interact. The nature and degree of discrimination
observed generally depended on the nature and degree of connectedness between individuals.
The behavioural patterns we observed across the four main results showed that the closer
people are the more they trust each other. Religious ingroup effects on beliefs carry over
strongly to actions, in contrast to the weaker effect when religiosity was known but
religious affiliation was unknown, and when religious affiliation was known (but) to be of
a different creed. These effects increased with one׳s religiosity, which is an indicator
of how rooted one is in a particular social group. We believe that the diversity in our
participant pool lends our results good domain validity. Our study is general, as opposed
to creed-specific, also in its explanation for how religion affects behaviour. In addition
to the evidence relating to our hypotheses we generally found that people are willing to
pay for the chance to discriminate, be it for statistical or taste motives. We designed an
incentive-compatible measure of the willingness to discriminate which was shown to be
significantly related to our other variables. We believe that our measure may be deployed
in other social identity contexts to guide policy related to discrimination in labour
markets and other specific areas.


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<ART>Representative evidence on lying costs
======================================

Authors: Johannes Abeler, Anke Becker, Armin Falk
DOI: 10.1016/j.jpubeco.2014.01.005
Year: 2014  |  Pages: 96-104
ASJC codes: 2002, 2003
Keywords: Lying costs, Private information, Representative experiment, Tax morale

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

A central assumption in economics is that people misreport their private information if this is to their material benefit. Several recent models depart from this assumption and posit that some people do not lie or at least do not lie maximally. These models invoke many different underlying motives including intrinsic lying costs, altruism, efficiency concerns, or conditional cooperation. To provide an empirically-validated microfoundation for these models, it is crucial to understand the relevance of the different potential motives. We measure the extent of lying costs among a representative sample of the German population by calling them at home. In our setup, participants have a clear monetary incentive to misreport, misreporting cannot be detected, reputational concerns are negligible and altruism, efficiency concerns or conditional cooperation cannot play a role. Yet, we find that aggregate reporting behavior is close to the expected truthful distribution suggesting that lying costs are large and widespread. Further lab experiments show that this result is not driven by the mode of communication. © 2014 The Authors.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Situations with asymmetric information are ubiquitous. Most of economic theory assumes
that people misreport their private information if this is to their material benefit;
behavior is only determined by the trade-off between financial gains from misreporting and
monetary fines when misreporting is detected.1 In contrast, many recent models in various
domains of Public Economics (and in Economics more generally) rely on the assumption that
people can experience a psychological disutility which holds them back from misreporting,
at least to some extent. These models invoke different underlying motives. Kartik et al.
(2014), for instance, assume that people face an intrinsic lying cost and show that in
this case the social planner can fully implement a much wider range of social choice rules
compared to the standard Maskin (1977) case without lying costs (see, e.g., Matsushima
(2008) and Dutta and Sen (2011) for similar assumptions). Many studies about incentive
systems for doctors assume that doctors are altruistic towards their patients and thus do
not always state the profit-maximizing diagnosis but rather treat patients honestly (e.g.,
Ellis and McGuire, 1986; Chalkley and Malcomson, 1998). The large literature on “tax
morale” (e.g., Lewis, 1982; Cowell, 1990; Andreoni et al., 1998; Slemrod, 2007; Torgler,
2007) demonstrates that many tax payers misreport their income only a little bit or not at
all. This literature is usually agnostic about the exact underlying motives but some
studies cite efficiency concerns (e.g., Alm et al., 1992), patriotism (Konrad and Qari,
2012), religiosity (Torgler, 2006), fairness (Bordignon, 1993), conditional cooperation
(Traxler, 2010) or honesty (Erard and Feinstein, 1994). To further improve these models
and to provide an empirically-validated microfoundation, it is crucial to understand the
relevance of the different potential motives. Additionally, understanding these motives
could inform the design of more psychologically-realistic policies, e.g., in the area of
tax enforcement, that have a higher potential of being successful. In this paper, we focus
on intrinsic lying costs and investigate how widespread and how large lying costs are. The
ideal data set to answer these questions would allow studying lying costs for a
representative sample of the population and in an environment without the confounding
effects of strategic interaction (including the levy of fines), reputational or efficiency
concerns, or altruism. So far, the best evidence on lying costs comes from experiments
conducted in tightly controlled laboratory situations. A robust result is that many
subjects misreport their private information to their own advantage but that a substantial
share of subjects refrains from reporting the payoff-maximizing type and that some are
fully honest (e.g., Gneezy, 2005; Charness and Dufwenberg, 2006; Fischbacher and Föllmi-
Heusi, forthcoming; de Haan et al., 2011; Houser et al., 2012; Shalvi et al., 2011; Wibral
et al., 2012; Serra-Garcia et al., 2013). These studies are a strong first indicator that
lying costs influence behavior. However, lab experiments do not allow for inferences with
respect to the prevalence of lying costs in the overall population since they have been
conducted almost exclusively with student samples (DellaVigna, 2009; Falk and Heckman,
2009). Also, decision making took place in an austere laboratory environment which might
trigger behavior representative only of certain non-lab situations. It could thus be that
there are systematic differences between behavior of students in the laboratory and
behavior of non-student subjects outside the lab. To circumvent these limitations, we
measure how people report their private information outside the laboratory by calling
participants on the phone at their home. Participants were drawn randomly from the German
population, yielding a representative sample. An incentivized experiment was embedded in
the interview. The experimental setup is related to the design of Fischbacher and Föllmi-
Heusi (forthcoming) and is extremely simple: participants were asked to toss a coin and
report their type, i.e., either “heads” or “tails”. Reporting tails yielded a payoff of 15
euros, which participants could choose to receive in cash or as an Amazon gift
certificate, while reporting heads yielded a payoff of zero. Participants thus had a clear
monetary incentive to report tails regardless of their true type. It was obvious that the
true outcome was only known to the participants, as they tossed the coin privately at
home. In this setup, we cannot draw reliable conclusions about the truthfulness of any
individual report. But we can learn about aggregate behavior by comparing the distribution
of reports to the true distribution of a fair coin (50% tails) and to the payoff-
maximizing distribution (100% tails). This indirect observation therefore allows us to
study the behavior of subjects in a situation in which private information is kept truly
private and in which subjects do not face any risk of detection.2 Moreover, the decision
is non-strategic; altruism does not play a role as the money is not taken from any
individual person; and reputational concerns are minimized since the interviewer is a
stranger with whom no future interaction can be expected. If all our participants were
rational money maximizers, we would expect that all of them reported tails. If behavior on
the phone was similar to previous comparable laboratory experiments (e.g., Houser et al.,
2012), we would expect about 75% of subjects reporting tails. In contrast to these
predictions, observed behavior does not statistically differ from everybody reporting
honestly. If anything, participants report the payoff maximizing outcome less often than
expected under truthful reporting. This latter effect, however, is small and disappears in
a second treatment in which participants were asked to report the total number of tails in
four consecutive coin tosses and received 5 euros times the number of reported tails. The
resulting distribution of reports in the 4-Coin Treatment is indistinguishable from the
distribution under complete truth-telling. Moreover, while previous studies (e.g., Dreber
and Johannesson 2008) have found correlations between individual characteristics, like
gender, and truth-telling, we do not find any robust correlations between individual
characteristics and reporting behavior. This is not surprising if almost all participants
report truthfully. Reports are solely determined by chance, namely the coin toss, which
cannot be related to any individual characteristic. Our results thus show that lying costs
are pervasive and are influencing behavior regardless of gender, religious beliefs,
education, or age. We complement our telephone study with two additional control
treatments in the laboratory to better understand what shapes lying costs, in particular
the effect of the mode of communication. In both lab treatments subjects reported the
outcomes of four consecutive coin tosses. Incentives were the same as in the 4-Coin
Treatment in the telephone study: 5 euros times the numbers of tails reported. In the
first lab treatment, subjects had to report the outcome directly to an interviewer via the
phone, mirroring our telephone study. We observe the same pattern of behavior as in
previous lab experiment: subjects lie much more than in the telephone study. In the second
control treatment, subjects reported the outcomes by clicking a number between 0 and 4 on
the computer screen as in most previous lab experiments. We find that subjects who enter
their report by clicking report slightly higher numbers but this difference is not
statistically significant. The difference to the telephone study persists: the average
report in each lab treatment is higher than in the telephone study. This shows that the
mode of communication does not systematically influence reporting behavior strongly and is
not driving the widespread truth-telling in our telephone study. We also elicit beliefs
about the behavior of other participants and find in all four treatments that participants
believe others to lie more than they actually do. Older participants (correctly) believe
that lying is less prevalent. In the lab, higher beliefs are correlated with higher own
reports. We find no evidence that being a student has a significant impact on behavior, or
that the perceived time pressure on the telephone or the limited experience of the survey
participants with the abstract design of economics experiments played a role. Our paper
adds to the nascent literature studying lying outside the lab. Previous studies focused on
particular groups: Bucciol and Piovesan (2011) study a sample of children and find that
many of them lie, unless they are reminded to be honest; Cohn et al. (2013) study
prisoners and find that they become less honest when reminded of their criminal identity;
and Utikal and Fischbacher (2013) ask a small sample of nuns to report the roll of a dice
and find significant downward lying. Studies looking at unethical behavior in less
abstract environments include Azar et al. (2013) who find that the majority of customers
in a restaurant do not return excessive change. Similarly, Bucciol et al. (2013) study
free-riding in public transportation in Italy and find that 43% of passengers evade the
fare. We add two features: we study a representative sample and we can investigate the
underlying motives by conducting additional lab experiments using the same well-defined
decision. Taken together, our results strengthen the doubts that previous lab experiments
have cast on the assumption of zero lying costs: we find evidence for even higher lying
costs in the telephone study. This suggests that studying the theoretical implications of
such costs (e.g., Kartik et al., 2007, 2014; Doerrenberg et al., 2013) is a promising
research avenue. At the same time, it is very likely that altruism, efficiency concerns,
etc. are also important factors in the decision to pay taxes or how to treat patients, for
example. Future research would need to investigate the relative importance of different
motives that hold people back from misreporting and the interactions between motives. Our
results also do not mean that lab experiments are uninformative about non-laboratory
settings. However, the difference in behavior between our telephone study and our previous
lab experiments rather shows how malleable reporting behavior can be. This opens many new
questions about how exactly reporting private information depends on the decision-making
context. Intuitively, different norms might apply when making such a decision at home,
representing a private and familiar environment. Similarly, people could be more attentive
to their own moral rules, e.g., abstaining from lying when at home.3 Irrespective of these
differences between lab and field, our study establishes that lying costs are more
important than previously assumed and are strongly influencing behavior across different
decision environments. In the next two sections, we present the design of the study and
our hypotheses. Section 4 contains the results. We discuss policy implications in Section
5.

<h>DESIGN</h>
------

The computer-assisted telephone interviews were operated by the Institute for Applied
Social Sciences (infas), a private and well-known German research institute. They were
conducted between November 2010 and February 2011.4 The average interview lasted 20 min
(standard deviation: 5.5 min). Telephone numbers were selected using a random digit
dialing technique: numbers were generated randomly based on a data set of all potential
telephone numbers in Germany. Only landline numbers were used in this study, as 92.7% of
German households have a landline number (Destatis, 2012). The selection of the
participant within each household was also random: only the member of the household whose
birthday was the most recent among all household members was eligible to participate. We
restricted participation to those aged between 18 and 70 years at the time of the
interview.5 The survey was split into two parts. The first part of the questionnaire
consisted of questions relating to the participants' socio-demographic background and
their risk and trust preferences. Risk and trust preferences were measured by using
subjective self-assessments, using the general risk question of the GSOEP (“How do you
consider yourself? Are you in general a rather risk-loving person, or do you try to avoid
risks? Use a scale from 1, meaning that you are not at all willing to take risks, to 7,
meaning that you are absolutely willing to take risks.” (Dohmen et al., 2011)) and the
World Value Survey trust question (“Generally speaking: Do you think one can trust other
people, or that one should rather be careful when dealing with other people? Please
indicate your answer on a scale from 1 to 7, with 1 meaning that one should be careful
when dealing with other people, and 7 meaning that one can trust other people.”). After
this part, the experiment described below took place. After the experiment, participants
were asked about their political preferences, their current living and financial
situation, their religious beliefs, and their attitudes towards opportunistic behavior and
everyday crime. At the very end of the interview, participants were asked to state their
belief about other participants' behavior in the experiment. Before the experiment started
the participant was reminded that the resulting data would be anonymized, and that infas
and the University of Bonn guaranteed the correct payment. The interviewer then asked the
participant to take a coin and explained the rules of the experiment: the task was to toss
the coin and report whether heads or tails came up.6 If the participant reported heads,
they received no payment. If the participant reported tails, they would receive 15 euros.
Then, the participant was asked to toss the coin and report the outcome. We will call this
treatment “1-Coin-Telephone.” 658 people participated in this version of our experiment. A
translation of the exact experimental instructions can be found in Online Appendix A. In a
second treatment, 94 people were interviewed and participated in the following variation
of the experiment. Participants were asked to take a coin, toss it four times, and report
the number of times that tails came up. For each time participants reported tails they
received 5 euros. Thus, they could earn 0, 5, 10, 15, or 20 euros. We will call this
treatment “4-Coin-Telephone.” Payment in both treatments could be received either in cash
via regular mail or as an Amazon gift certificate code. The alphanumeric 14-digit gift
certificate code was transmitted via email or directly on the phone at the end of the
interview. In order to further investigate what influences behavior in the telephone
study, in particular the mode of reporting, we additionally conducted two versions of the
4-Coin Treatment in the laboratory. Subjects were students of the University of Bonn
studying different majors except Economics. They were seated at a desk with a computer in
separate room-high cubicles closed off by curtains. As the experiment took only a few
minutes, it was run at the end of the sessions of a different experiment (similar to
Fischbacher and Föllmi-Heusi, forthcoming). In the preceding experiment subjects made
abstract consumption or labor supply choices which involved no private information and no
interaction with other subjects. When the experiment started, subjects were asked to take
a coin that was placed in their cubicle, toss it four times, and report how often tails
came up. For each time they reported that tails came up they received 5 euros, i.e., up to
20 euros, just like in 4-Coin-Telephone. Their earnings were paid in cash directly after
the experiment.7 The only difference between the two lab treatments was how the reporting
was done. In the first treatment, subjects had to state their report directly to an
interviewer via the phone, mirroring our telephone study. After tossing the coin in their
cubicle, they were asked to go one-by-one to an adjacent room and pick up the telephone
that we had placed there. An interviewer on the other side of the line (whom subjects
never met directly) would then ask for their experimental ID and the number of times the
coin showed tails. We made sure that other subjects could not hear the conversation. The
starting times for the coin tossing was staggered, such that subjects did not have to wait
between coin-tossing and reporting. 170 subjects participated in this treatment which we
will call “4-Coin-Lab-Tel.” This treatment serves to replicate our telephone study as
closely as possible in the laboratory. In the second treatment, subjects reported their
outcome by clicking a number 0 to 4 on the computer screen, similar to previous lab
experiments. 180 subjects participated in the second treatment which we will call “4-Coin-
Lab-Click”. This treatment serves to investigate whether the mode of communication, i.e.,
clicking on a computer screen versus reporting to a person via the telephone, influences
reporting behavior.

<h>HYPOTHESES</h>
----------

The standard economic prediction in our setup is straightforward: depending on the
treatment, people will report tails one or four times, respectively. This is the payoff
maximizing outcome as there are no exogenous costs linked to misreporting, no possibility
of detection and no fines. The setup is extremely simple and participants should have no
trouble identifying the payoff maximizing choice. Moreover, the setup is highly anonymous,
discouraging any reputational concerns because of repeated interaction. If, however, some
participants incur a psychological cost or derive direct disutility from falsely reporting
their private information per se we should expect both heads and tails to be reported in
the experiment. There are a few recent theoretical papers that assume such a cost. For
example, Kartik (2009) and Kartik et al. (2007) build on Crawford and Sobel's (1982)
cheap-talk model and derive predictions for the case that some agents incur costs when
misreporting their private information (see also, e.g., Saran, 2011; Kartik et al., 2014).
Assuming some degree of heterogeneity in the incurred costs when misreporting, it is then
a question of the trade-off between psychological costs and monetary benefits of
misreporting how many participants will report heads and how many report tails.
Participants in 1-Coin-Telephone have to make a clear, binary choice whether to lie or
not; if lying costs are related to self-reputation or identity (e.g., Bénabou and Tirole,
2006; Akerlof and Kranton, 2000), lying in such a setting could impact self-reputation or
identity more and thus make lying more costly. Participants in 4-Coin-Telephone can make a
finer choice between being honest, exaggerating a little bit, or lying maximally; this
could render small lies compatible with a positive self-reputation and thus enhance lying
(Mazar et al., 2008). Such non-maximal lying has already been shown to be important by
Fischbacher and Föllmi-Heusi (forthcoming). In the telephone study, participants tossed
the coin at their home. It was thus obvious that the interviewer could not secretly
observe the true outcome of the coin toss.8 If some participants in our lab experiments
(erroneously) believed that the experimenter could observe the true outcome and believed
(again erroneously) that misreporting would lead to some negative or unpleasant outcome,
we would expect more truth-telling in the laboratory.9 Regarding potential differences in
reporting behavior according to individual characteristics, we would expect that women are
more honest than men (as already shown by Dreber and Johannesson, 2008; Houser et al.,
2012). More religious participants would be expected to be more honest, since religious
priming leads to less lying and more pro-social behavior (Mazar et al., 2008; Shariff and
Norenzayan, 2007). Income could be positively correlated with honesty because of the lower
marginal utility of the monetary rewards or negatively correlated because of reverse
causality. A similarly ambiguous hypothesis can be derived for education or the social
environment, e.g., the size of the community or family status. Along theories of
endogenous social norms (e.g., Traxler 2010; López-Pérez, 2010, 2012), we would expect
that higher beliefs about the reporting of other participants are correlated with own high
reporting.

<hs>  Telephone study</hs>
  ~~~~~~~~~~~~~~~

In 1-Coin-Telephone, the distribution of actual reports is very close to the truthful
distribution; participants report the payoff-maximizing outcome slightly less often than
expected if everyone reported truthfully. In 4-Coin-Telephone, the distribution of reports
is indistinguishable from the truthful distribution. Fig. 1 illustrates aggregate behavior
(the dashed line corresponds to the expected distribution if every participant reported
the true outcome of the coin toss). 55.6% of participants report heads as the outcome of
the coin toss, yielding a payoff of zero, the remaining participants report tails yielding
a payoff of 15 euros. The payoff-maximizing outcome is reported slightly less often than
in 50% of the cases and although the difference is small in terms of effect size, it is
significant (Binomial test, p = 0.004) Fig. 2 shows aggregate behavior in 4-Coin-
Telephone. Again, reporting behavior follows the expected distribution under complete
honesty very closely (the dashed line corresponds to the truthful distribution). In fact,
the distribution of reported outcomes is statistically indistinguishable from the truthful
distribution (Kolmogorov–Smirnov test, p = 0.61; binomial tests of the expected against
the observed frequency, all five p > 0.13). In particular, and unlike in 1-Coin-Telephone
where “too many” people report the payoff-minimizing outcome, there is no significant
over-reporting of zero in this treatment.10 Looking at behavior in both treatments we can
therefore summarize that the payoff-maximizing outcome is reported by much fewer
participants than expected if no one incurred lying costs. It is also reported less often
than suggested by previous lab experimental studies, which find some truth-telling but
also many instances of the payoff-maximizing report. Instead, it is close to the
distribution that would arise if every participant reported his or her type truthfully.11
Previous studies have shown that truth-telling correlates with observable characteristics,
e.g. gender or religiosity (Dreber and Johannesson, 2008; Houser et al., 2012; Mazar et
al., 2008; Shariff and Norenzayan, 2007). In contrast, if our conjecture that almost all
participants report truthfully is correct, an individual's reported outcome will only be
driven by their random coin toss; if this is the case, reporting cannot be correlated with
any individual characteristic, as these are orthogonal to the chance move. Therefore, if
we do not find such a correlation, our finding of (almost) complete honesty is supported.
More specifically, we conduct regression analyses for the two experiments in order to
examine whether there are systematic effects of individual characteristics on reporting
behavior. First, we regress the report only on clearly exogenous variables such as age and
gender, in a second step adding religious denomination. We then include income, the size
of the city the individual lives in, and education dummies. Finally, we look at the effect
of an individual's religiousness (interacted with denomination), their risk and trust
preferences, and their belief about the reporting behavior of other participants. There is
no significant correlation between reporting behavior and any individual characteristic.
First, we look for potential group differences in terms of reporting behavior in 1-Coin-
Telephone by conducting Probit regressions of the reported outcome on the respective
characteristics (see Table 2 in Online Appendix E). No characteristic except for one's
belief about others' behavior is significantly associated with reporting in the
experiment: participants who think many other participants report tails dishonestly, are
less likely to report tails themselves. This belief is, however, not significant if we
include it as the only explanatory variable (p = 0.15). Note in particular that neither
gender nor any religion-related variable is significantly correlated with reporting.
Conducting the same regressions as in Table 2 using OLS leaves the results unchanged.
Next, we check whether these results also hold in 4-Coin-Telephone. We run Ordered Logit
regressions of the reported number of tails on the same explanatory variables as before.
Table 3 in the online appendix illustrates the results from this estimation. Only the
coefficient for trust is significant. This effect is, however, not robust to the inclusion
of other explanatory variables. The effect is also not present in 1-Coin-Telephone. In
contrast to 1-Coin-Telephone, the belief coefficient shows no significant association with
reporting behavior in this treatment and the point estimate has the opposite sign. We will
discuss the data on beliefs in more detail in Section 4.3. Two further aspects of our
analysis are worth noting. First, when running OLS regressions using the same predictor
variables as above, we find that only two of the 10 specifications have an adjusted R2
above 0 (below 0.004), all other adjusted R2 values are negative. Moreover, the resulting
adjusted R2 tends to decrease in the number of included variables. This again underlines
our conclusion: the tested predictor variables do not increase explained variance in the
dependent variable compared to pure chance. Second, we also test the correlations between
reported number and answers to the survey questions that we did not include in the main
specifications of Tables 2 and 3. These include a person's citizenship and country of
birth, various personal characteristics, a person's current job or educational situation
and their current or recent position in the professional hierarchy, a person's willingness
to tell white lies in different situations, a person's family status and living situation
(whether one lives with a partner and the number of people belonging to the household),
the frequency of church attendance, a person's political preference, and the individual's
tendency to behave in an opportunistic way as well as the belief about others' willingness
to behave like that. Testing these variables as predictors in Probit and Ordered Logit
regressions in the two different data sets, akin to Tables 2 and 3, we find no robust
association between any of them and reporting behavior. In particular, this means that
students and non-students do not behave differently in our sample. This holds when we
consider current students or include former students as well (Kolmogorov–Smirnov tests,
all p > 0.409). It is thus not a student vs. non-student difference, e.g., a difference in
education, age, cognitive skills, or socio-demographic background, which drives the
difference between our results and previous lab experiments. Summing up, the overall
picture is confirmed: no individual characteristic, whether exogenous or endogenous, is
systematically associated with reporting behavior suggesting that almost all participants
in our study tell the truth. It could still be that a subgroup of people, which we cannot
identify with our background information, reports tails more often than actually true
while another subgroup reports tails less often. This could result in the two effects
offsetting each other, which would result in a similar picture of aggregate behavior.
However, we consider this to not be likely as our analysis shows that this is not the case
for any of the numerous subgroups that we can identify with our data. More importantly,
such an effect would further need to recreate the distinct distributions of Figs. 1 and 2
which is implausible.

<hs>  Laboratory experiment</hs>
  ~~~~~~~~~~~~~~~~~~~~~

To further investigate the motivations underlying behavior in the telephone study, we
conducted two 4-Coin Treatments as laboratory experiments. We will first discuss the
4-Coin-Lab-Tel treatment which keeps the mode of communication as in the telephone study:
subjects had to report their result over the phone directly to an experimenter.12
Subsequently, we compare this treatment to 4-Coin-Lab-Click, in which subjects reported
their number by clicking a button on a computer screen as in previous lab experiments.
This second comparison will allow us to disentangle the influence of the mode of
communication.13 Subjects in 4-Coin-Lab-Tel report substantially higher numbers than
subjects in 4-Coin-Telephone. The upper panel of Fig. 3 shows aggregate behavior in
4-Coin-Lab-Tel: most subjects refrain from reporting the maximal outcome, forgoing on
average 6.82 euros, quite a considerable amount compared to the average hourly student
wage in Germany of about 10 euros. At the same time, behavior is significantly different
from the distribution expected under truthful reporting, the dashed line in the figure
(Kolmogorov–Smirnov test, p < 0.001; binomial tests, all five p < 0.009). This replicates
previous findings in the lab: many subjects lie but often not maximally. Reporting
behavior also deviates strongly from what we have observed in the telephone study: reports
are significantly higher in 4-Coin-Lab-Tel than in 4-Coin-Telephone. In Table 1, columns 1
and 2, we regress the reported number of tails on a dummy for being in the lab, a dummy
for 4-Coin-Lab-Click and controls for age and gender. The lab dummy is highly
significant.14 We find the same result if we compare 4-Coin-Telephone and 4-Coin-Lab-Tel
using a two-sample Kolmogorov–Smirnov test (p < 0.001). These results demonstrates that
our 4-coin randomization mechanism does not drive the truthful behavior in 4-Coin-
Telephone and that, by moving our telephone setup to the laboratory, we are able to
strongly change behavior (as we showed within the telephone study, this is not driven by
subjects being students per-se). How big is the additional effect if we also change the
mode of communication? Subjects in 4-Coin-Lab-Click report slightly higher numbers than
subjects in 4-Coin-Lab-Tel but this difference is not statistically significant. Only the
report of 4 occurs significantly more often in 4-Coin-Lab-Click; the reports of 0, 1, 2,
and 3 are not different across treatments. Reports in 4-Coin-Lab-Click are significantly
higher than in 4-Coin-Telephone. The lower panel of Fig. 3 shows aggregate behavior in
4-Coin-Lab-Click. The distribution of reports is very similar to the one in 4-Coin-Lab-
Tel, the average report being only slightly higher (2.78 in Click vs. 2.64 in Tel). The
overall distribution and the average report are not significantly different across the two
treatments (two-sample Kolmogorov–Smirnov test, p = 0.136; Ordered Logit in Table 1,
columns 1 and 2, both p > 0.096). The share of subjects reporting 0, 1, 2 or 3 are also
not significantly different (tests of proportion, all p > 0.100). However, subjects in
4-Coin-Lab-Click report 4 significantly more often (p = 0.007).15 At the same time,
behavior in 4-Coin-Lab-Click is markedly different from 4-Coin-Telephone (two-sample
Kolmogorov Smirnov test, p < 0.001, Ordered Logit in Table 1, columns 1 and 2, F-test,
both p < 0.001). Overall, our data thus show that the mode of communication does not have
a strong effect on behavior and cannot explain the difference between our telephone study
and previous lab experiments. This result is further confirmed by Waubert De Puiseau and
Glöckner (2012) who also find considerable truth-telling at home, though not as extreme as
in our data, using an online panel in which participants answered questions at home by
clicking on a computer screen. Houser et al. (2012) conduct a 1-coin lab experiment and
find similar levels of lying as in our lab experiments, replicating the other side of our
results. One could think that one reason why behavior in the telephone study differs is a
perceived time pressure on the telephone which might make lying more difficult. However,
we measure response times in the laboratory and do not find a correlation with the report
(Ordered Logit, p = 0.108).16 If anything, the report in the lab is higher for short
decision times. This mirrors results of Shalvi et al. (2012) who impose exogenous time
pressure in a similar lab experiment and who find that subjects become less honest under
time pressure. Taken together, these results suggest that behavior in the telephone study
is not driven by perceived time pressure. We also find no correlation of the number of
previous participations in other lab experiments with reporting behavior in the lab (p =
0.578), suggesting that the limited experience participants of the telephone study have
with the abstract design of economics experiments does not play a role. It rather seems
that different norms apply when making a reporting decision at home, representing a
private and familiar environment, compared to in the lab where other, more selfish norms
might be triggered.17 We showed above that women do not report differently from men in the
telephone study. As one can see from Table 1, women do report lower numbers in the lab.
This effect is only weakly significant in the sample of all three 4-Coin Treatments, i.e.,
also including 4-Coin-Telephone which dilutes the effect, and becomes significant if we
restrict the sample to the two lab treatments (p = 0.027 and p = 0.046 in regressions akin
to columns 2 and 4 of Table 1).

<hs>  Beliefs about other participants</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Previous studies (e.g., López-Pérez, 2010; Diekmann et al. 2011) have investigated the
relationship of reporting behavior and the beliefs about what other people report. Since
our telephone and lab settings generate strong differences in reporting behavior, we next
examine whether there is a similar difference in beliefs and whether this could help
explain the differences in behavior. In all four treatments, we elicited beliefs about the
reporting behavior of the other participants. We will mainly focus on analyzing beliefs in
the 4-Coin Treatments as the outcome variable is richer and we have additional treatments.
In the 4-Coin Treatments, subjects were asked two questions regarding their beliefs about
the behavior of other subjects in their treatment (the question referred to 1000
participants in 4-Coin-Telephone): “We are conducting this experiment also with 100 other
participants. How many of these 100 participants do you think report tails more often than
they actually tossed?” and “How many of these X overreporting participants do you think
report that they tossed tails in each of the four coin tosses?”18 We will use the answers
as direct measure of the belief about the share of liars and about the share of maximal
liars. Using a very simple model, we can also combine the two answers to back out the
implied belief about the average report in the population or the share of participants
reporting the payoff-maximizing outcome. The model assumes, similar to Kartik (2009) and
Mazar et al. (2008), that participants expect others to face a psychological lying cost
which is increasing and convex in the size of the lie and which might be heterogeneous
between participants. Online Appendix D describes the model and the belief measures in
more detail. In all treatments, participants believe others to overreport more than they
actually do. Fig. 4 compares average beliefs with average actual behavior for each
treatment. We take as variable of interest the share of participants who report the
payoff-maximizing outcome, i.e., 4 tails in the 4-Coin Treatments and tails in 1-Coin-
Telephone. Since we expected participants to be unfamiliar with the true distribution of
the sum of four coin tosses, we didn't ask directly for their belief about this share. We
are able to calculate it, given the assumption of convex lying costs, from the two
questions for the 4-Coin Treatments: it is the share of liars who report 4 (question 2)
plus the share of honest 4's (the probability of a true 4 times (1 — answer 1)). Since we
do not observe whether an individual overreports we cannot directly compare the two
answers to actual behavior.19 We find in all four treatments that participants believe
that others overreport more than they actually do. The differences are highly significant
(t-tests, all p < 0.001). The same results obtain when we consider the average reported
number as variable of interest.20 What shapes these beliefs? Older participants believe
others to overreport less. Participants expect more overreporting when participants can
enter their report by clicking on the screen. In Table 1, columns 5 and 6, we regress the
answer to the second question on treatment dummies, a gender dummy and age (the table only
considers the 4-Coin Treatments). We find that subjects in 4-Coin-Lab-Click believe others
to overreport more than subjects in 4-Coin-Lab-Tel. Being in the laboratory seems to
increase beliefs (column 5) but this effect goes away once we control for age (column 6).
Participants in the telephone study are on average much older than the student sample in
the lab and older participants expect others to overreport less. This means that the
beliefs of older participants in the telephone study are closer to actual behavior than
the beliefs of younger participants. The same effect of age is present in 1-Coin-Telephone
(p < 0.001). Using the answer to the first question, or the belief about the average
report or the belief about the share of participants reporting 4 does not change any of
the results. In the lab, participants who believe that others report high numbers also
report higher numbers themselves. We discussed above that there is no robust correlation
between reports and beliefs in the telephone study. In Table 1, columns 3 and 4, we study
the correlation of reports and beliefs for the 4-Coin Treatments in lab and field. We
regress the reported number of coin tosses on treatment dummies, controls for gender and
age and on the answer to the second belief question. We find that participants who believe
others to report high numbers also report higher numbers themselves. If we exclude 4-Coin-
Telephone from the analysis, the coefficient on the belief variable becomes even bigger
and stays significant. One could interpret this finding as yet another indication that
almost all participants are honest in the telephone study because, if some were not, we
should also find a correlation with beliefs in the telephone study (similar to the gender
effect we do not find). Furthermore, since beliefs are on average higher in 4-Coin-Tel-
Click, the difference between the two lab treatments – which is barely significant in
column 1 – becomes even smaller once we control for beliefs. These results are again
robust to the exact belief measure we use. The direction of causality between beliefs and
behavior is obviously unclear in our setting. On the one hand, it could be that a high
belief induces participants to also report higher numbers. This would be in line with a
notion that moral norms are endogenous to the beliefs people hold about the behavior of
their peers (see, e.g.,Traxler, 2010; López-Pérez, 2010, 2012). Diekmann et al. (2011)
provide causal evidence that higher beliefs lead to higher reports. If this is the
mechanism for the correlation between beliefs and behavior, it is even more surprising
that participants, in particular in the telephone study, decided to refrain from
exploiting the opportunity to receive a considerable amount of money when they believed
that many others would do so. On the other hand, the causality might run in the opposite
direction if participants ex-post justify their own high report with a stated belief that
others also overreport.

<h>CONCLUSION</h>
----------

Using a representative sample of the German population we conducted telephone interviews
during which respondents participated in an incentivized experiment. Depending on the
treatment, they could earn money by reporting tails as the outcome of one or four coin
tosses. We find that almost all participants report their coin toss(es) honestly: the
distributions of reports are extremely close to the true distribution of a fair coin toss
or four coin tosses, respectively. Moreover, reports are not correlated with any
individual characteristic, including gender which has been shown to predict honesty in
previous lab studies. We conducted additional laboratory experiments to study the motives
underlying the behavior on the phone. While reports are generally higher in the lab than
in the telephone study we find little evidence that the mode of communication (reporting
directly to someone via the phone vs. clicking a number on a computer) influences
behavior. Being a student has also no effect. Our results underline doubts about the
generalizability of economic models which assume that people always lie maximally when it
is financially beneficial. Apparently, people do not only care for the trade-off between
financial gains from misreporting and the monetary fines when misreporting is detected
(cf. Becker, 1968). Our results instead support models like Erard and Feinstein (1994),
Kartik et al. (2014) or Doerrenberg et al. (2013) which assume that many people do not lie
or do not lie maximally; intrinsic lying costs could be a potential microfoundation for
these and similar models. The effect of patriotism and religiosity on tax morale (Konrad
and Qari, 2012; Torgler, 2006), for example, could also work through an increased lying
cost. The strong differences we find between telephone and lab environment suggest that
lying costs are stronger in our setting outside the lab. It seems that different norms
apply when reporting private information at home. Similarly, it might be that the familiar
and intimate environment of one's own home reinforces one's personal identity and renders
personal moral standards more salient. This is in line with recent evidence by Cohn et al
.(2013) who conduct a similar experiment with prisoners. They find that priming prisoners
with their criminal identity reduces honesty. Lab experiments, in turn, could be more
representative of decisions for which people take on a particular role or identity in
addition to their private identity. At the same time, this study does not imply that
everybody always reports their private information truthfully. The level of lying costs
seems rather to be influenced by the context in which people are asked to report their
type (see also Mazar and Ariely, 2006; Mazar et al., 2008). The difference in behavior on
the phone and in the lab shows how malleable reporting behavior can be. Our results
therefore point to important policy implications: institutions, e.g., tax authorities,
could make use of the context dependence of reporting behavior when designing decision-
making environments. As we find strong evidence for widespread lying costs, appropriate
mechanisms might be much less complex than those resulting when assuming that agents have
no qualms about lying. It might be possible to change reporting behavior in simple and
low-cost ways in the spirit of libertarian paternalism (Thaler and Sunstein, 2003).
Further research is necessary to uncover what the crucial aspects of the decision-making
environment are that induce truth-telling.


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<ART>Self-serving invocations of shared and asymmetric history in negotiations
=========================================================================

Authors: Linda Dezső, George Loewenstein
DOI: 10.1016/j.euroecorev.2019.103309
Year: 2019
ASJC codes: 2002, 2003
Keywords: Asymmetry, Bargaining impasse, Fairness, History, Self-serving beliefs

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

The existence of an asymmetric history between bargainers can trigger self-serving beliefs about the fair settlement of a subsequent dispute, ultimately leading to bargaining impasse. In a two-stage bargaining experiment we demonstrate that dyads who share a history that produced wealth asymmetries between them are less likely to settle in a subsequent negotiation than when the same wealth asymmetry stems from negotiators’ independent histories. When negotiators share an asymmetric history, the individual who previously lost out in the first stage believes that s/he deserves compensation in the second stage, but the individual who prevailed in the first stage believes that compensation is not warranted. These divergent, self-serving views about a fair settlement – and the resulting irreconcilable demands – lead to bargaining impasse. We find, further, that unbiased judges side with the losers in the first stage; they believe that it is fair for them to be compensated in the second stage. Indeed, this is true, albeit to a lesser extent, even if the winner and loser had not directly interacted with one another – i.e., if their history is not shared.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Examples of a dispute in which one party self-servingly invokes the past – for example,
that one put in a lot of overtime to meet a recent project deadline and thus deserves some
“late mornings” – are easy to call to mind. These situations are not just unique to
individuals. On the international stage, politicians often invoke history to justify
demands that conflict with those of other countries. In discussions of European refugee
quotas, for example, some argued that their country did not benefit from colonization of
the country from which refugees originated, and therefore they should bear a smaller
fraction of the burden of the refugee quota. Needless to say, such claims were rejected by
leaders of the countries that had participated in, and likely benefited from, such
colonization. Differences in the relevance of historical carbon emissions between
developed and developing countries likewise complicate climate change negotiations over
different countries’ fair burden in reducing greenhouse emissions. These are examples of a
large spectrum of disputes that are intensified by, and in some cases specifically revolve
around, self-serving views about the implications of the past for a current situation. At
issue is whether and to what extent one party's prior outcome should have a bearing on the
fair division of current resources. We are specifically interested in situations in which
one party (the “loser”) lost to another party (the “winner”) in a previous allocation of
resources. We ask whether, when the same parties enter into a new negotiation, each party
views compensation for the prior loss as fair, and the extent to which divergent views
about the implication of the past for the fair settlement of the current dispute are
associated with increased likelihood of impasse. Although the history of interactions
between players has been examined in prior game-theoretical research, the focus has been
on strategic behavior to build reputation (e.g., Roth and Schoumaker 1983). By contrast,
our interest in history focuses on whether and how different sequences of prior outcomes
affect subsequent negotiations via divergent conceptions of fairness (e.g., Dezső et al.,
2015). We argue, and experimentally demonstrate, that whether there is a self-serving
invocation of an asymmetric history leading to impasse depends on whether negotiators’
wealth asymmetry stems from their shared (i.e., interdependent) or independent history. By
a shared asymmetric history, we mean a situation in which the winner specifically won out
over the loser in a prior distributive situation. In such situations, the disadvantaged
party may feel that the advantaged party benefited at his/her expense. By contrast, when
there is asymmetry from independent histories, one party was the winner and the other
party the loser in the prior interaction, but the winner did not win at the loser’s
expense. Results of our bargaining experiment demonstrate that when negotiators’ ex-ante
asymmetry is due to their shared histories, the loser believes that s/he deserves
compensation from the winner, but that the winner rejects this perspective. This
divergence of negotiators’ beliefs about the fair solution increases the likelihood that
they will fail to settle the subsequent negotiation. In contrast, when the winner's and
loser's histories are independent, they are likely to hold more convergent views of
fairness and be more likely to settle the current dispute. To obtain an impartial view of
fairness, unencumbered by self-serving bias, we recruited an independent sample of
subjects to provide an unbiased perspective on the fair solution to the dispute in the two
asymmetric conditions – i.e., in which the history between the parties is shared or
independent. As predicted, we find that the amount of compensation seen by these impartial
judges as fair is greater for losers when the asymmetry stems from negotiators’ shared
histories versus independent histories. Comparing players’ beliefs to those of the
unbiased judges, we find that when negotiators share an asymmetric history, the fairness
views of both winners and losers give the loser less than the amount judged as fair by the
impartial judges. However, the losers’ fairness judgments are closer to the impartial
judges than the winners’ judgments. When the histories are independent, on the other hand,
winners’ views of fairness coincide with the views of unbiased judges, but losers believe
they should be entitled to more compensation than do the impartial judges. In what
follows, we briefly summarize relevant literature. Then, we present the framework of the
bargaining experiment and our predictions. These are followed by a detailed description of
the methods. Next, we present the results of the experiment. We conclude with a discussion
of the broader implications of our findings.

<h>RELATED LITERATURE</h>
------------------

According to equity theory, people prefer outcomes of joint activities to be equitable,
meaning that rewards are proportionate to inputs, and, when they perceive inequity, will
engage in efforts at restoring equity (Adams, 1966; Homans, 1974). Equity theory is
supported by research showing that people who perceive themselves as having been treated
inequitably are more likely to lie and cheat in an effort task to restore equity. In
psychology, see, Gino and Pierce (2009), Greenberg (1993), John et al. (2014), Sharma et
al. (2014), for instance. In economics, see, e.g., Fehr et al. (1993) and Houser et al.
(2012). Greenberg (1993), for instance, reports that workers compensate themselves by
stealing from a company's inventory if they feel unfairly underpaid. Houser et al. (2012)
finds that people who received an inferior allocation in a dictator game, from a human
rather than a random device, are more likely to lie in a subsequent task to increase their
experimental earnings. In situations in which parties jointly create the to-be-divided
resources and the individual contributions are known, division proportional to
contribution is typically the salient norm, consistent with equity theory (Cappelen et
al., 2017, 2013a, 2007; Karagözoglu and Riedl, 2014; Konow, 2000). There are, however,
complex situations in which unequal contributions are due to uncontrollable factors such
as bad luck. The question of what constitutes equity arises here and sets the stage for
context-dependent views on a fair division (Konow, 2001). One solution is to compensate
the disadvantaged party through redistribution to the extent that her/his lower
contribution is caused by uncontrollable factors (Cappelen et al., 2013b; Fong, 2001;
Konow, 2001). The degree of freedom in deciding whether and how the asymmetry should be
dealt with, however, leads to the emergence of multiple fair solutions not only among
stakeholders (Thompson and Loewenstein, 1992) but also among neutral judges with no
personal interest in the distribution (Cappelen et al., 2007). As long as negotiators are
flexible in their claims, agreement is likely to occur. There are, however, situations in
which claims are fueled by inflexible and divergent beliefs about fairness (Birkeland and
Tungodden, 2014; Camerer, 2003). When notions about the fair settlement of a negotiation
are self-servingly biased, bargainers are convinced that their view of a fair settlement
coincides with the unbiased fair solution and they refuse to compromise (Babcock et al.,
1995; Birkeland and Tungodden, 2014; Konow, 2005). This central role of fairness beliefs
in negotiations has been advanced in a theoretical framework proposed by Birkeland and
Tungodden (2014). The authors incorporate fairness motives and the weights that people
attach to them, and generate predictions of bargaining outcomes in different situations.
Here, we focus on their proposition regarding principled disagreement, which occurs when
negotiators hold incompatible beliefs about what would be a fair settlement, and insist on
these beliefs to the point where they reach stalemate. In this paper, we combine the
research on compensation-seeking after experiencing a loss with that addressing the key
role in negotiation of beliefs about fairness. We ask whether a prior asymmetric
distributive outcome between negotiators would be more likely to lead to incompatible
beliefs about the fairness of compensation in a subsequent negotiation. Furthermore, we
ask whether this situation is more likely to lead to impasse when the asymmetry is due to
an allocation schema in which negotiators’ outcomes were interdependent than when their
outcomes were independent. Rather than creating asymmetries between negotiators via
lopsided potential contributions to the to-be-divided proceeds (as done, for instance, by
Cappelen et al., 2013a), we establish the asymmetry between negotiators with respect to
their initial wealth levels. Negotiators are subject to a lopsided allocation of proceeds
generated through a real-effort task in a prior distributive situation, and we test if
this history spills over onto their subsequent bargaining behavior. We view asymmetries in
the bargainers’ prior outcomes as a context for the focal negotiation, in which the
interpretation of the significance of the prior outcomes is likely to differ between them.
The loser is likely to believe that the prior outcome has a bearing on the fair
distribution, and that s/he is entitled to compensation. By contrast, the winner is likely
to believe that the past is irrelevant to the present and that the outcome of the
negotiation should depend only on factors relating to that negotiation. To the best of our
knowledge, only two previous studies address the impact of ex-ante asymmetries on
bargaining behavior. The first is a lab study from Camerer and Loewenstein (1993, Study 1
– Appleton-Baker). They demonstrated increased likelihood of impasse between buyers and
sellers who had the opportunity to renegotiate a sales transaction after their BATNAs
(best alternatives to negotiated agreement) were revealed. These BATNAs were treatment
variables, randomly assigned to subjects at the beginning of the experiment, and subjects
were not allowed to reveal them during the initial negotiation. After parties first
negotiated the sales prices, their BATNAs were revealed and they were prompted to
renegotiate the price. Here, the ex-ante asymmetry between bargainers arose from one party
benefiting more than the other from the initial sales transaction in the light of the
revealed BATNAs. The authors’ key finding is that pairs with greater ex-ante asymmetries
were more likely to reach impasse in the renegotiation. Those subjects who realized that
they made a disadvantageous initial deal upon BATNAs becoming public knowledge tried to
get compensation in the renegotiation. However, their claims were unwelcomed by their
bargaining partners who made advantageous initial deals. The authors speculated that this
is because negotiators hold self-serving views about the implication of their sales
histories on the current bargaining. Importantly, in this study, the ex-ante asymmetry was
not randomly assigned but rather was partly the outcome of the initial bargaining, raising
the issue of selecting for weak and strong bargaining skills. Therefore, it could not be
determined if the bargaining impasse was due to the initial asymmetry, or rather to a
factor that was associated with creating the asymmetry in the first place. In other words,
it is possible that the same characteristic accounts for weak negotiating skills that put
someone in an inferior position after the initial sales transaction and for later claiming
compensation upon learning how bad of a deal one made. Moreover, as the authors did not
elicit subjects' beliefs about the unbiased fair solution, one cannot tell whether and to
what extent stalemates were driven by divergent and potentially self-serving beliefs about
the fair compensation for the person who lost out in the initial transaction. The second
relevant study is Experiment 2 reported by Dezső et al. (2015). Here, the authors did
manipulate prior asymmetries between bargainers and found that when their asymmetric
histories are linked together, they are more likely to reach an impasse than when the
asymmetries are due to a prior interaction with another party. In this earlier study, as
in the current study, bargainers arrived at the table with asymmetric wealth levels due to
a previous, lopsided distribution of their joint proceeds. In the first stage of the
experiment, both subjects took the same trivia quiz, and each of their scores was added
together to determine total joint earnings. Then, the person who had obtained the higher
score received all the joint earnings and the person with the lower score received nothing
(in the event of a tie, the individual who received total earnings was determined by
chance). Then, in stage two of the same-partner condition, winners and losers remained
paired. However, in the different-partner condition, winners and losers were paired with
someone else – always ensuring winner-loser pairs. In both conditions, the asymmetry was
due to the winner having benefited at the expense of a loser, but, in the different-
partner condition, the winner benefited at the expense of a different loser than of
his/her stage two pair. The key finding from this study was that impasse was more likely
in the same- than different-partner condition. The authors speculate that this is because
losers and winners in the same-partner condition held incompatible views about the fair
compensation to the loser. This, however, could not be addressed because negotiators’
beliefs about the fair division were not elicited, so it was unclear whether, and to what
extent, impasses were driven by self-serving beliefs about a fair settlement. Furthermore,
negotiators in the Dezső et al. (2015) study were uninformed about their actual stage one
and two contributions (i.e., quiz earnings), obscuring whether they sought shares
according to the proportionality rule. Additionally, allocations in the first stage were
not random, but were determined by which individual got a higher score on the quiz. So
there was, as in Camerer and Loewenstein (1993), a connection between the personal
characteristics of the disputants (specifically, their skill at the task) and the outcomes
they experienced. Moreover, at the beginning of stage one, subjects were uninformed about
the forthcoming unfair allocation schema, which calls into question the extent to which
frustration, surprise, and relief may have influenced the observed bargaining behavior.
Finally, as fair divisions were not elicited from neutral judges, it is unclear if
redistribution is generally viewed as a fair solution between negotiators with asymmetric
histories. In addition to addressing the limitations of these previous two studies, we
examine the nature and role of beliefs about the fair settlement in bargaining between
parties with asymmetric history. To disentangle the effect of asymmetry from
interdependency (i.e., losing to a beneficiary), we manipulate whether asymmetric prior
wealth levels between bargaining dyads are due to histories that were shared, such that
only one party could win at the expense of the other, or independent, such that both could
have won or lost (in the event that one won and the other lost, the winner did not win at
the expense of the loser). We call the former the “shared asymmetric history condition”
and the latter the “independent asymmetric history condition.” We suspect that losers in
the shared asymmetric history condition view it as fair to obtain compensation from the
winner, but that compensation will be less of an issue in the independent asymmetric
history condition. To investigate whether the unbiased fair solution involves compensating
the loser for his/her prior loss, we employed a preliminary survey. Here we elicited
judgments from a sample of subjects drawn from the same population as those recruited for
the actual experiment. We described the experiment to them and asked them to take the
position of a neutral judge and to provide their views about what would be a fair division
of hypothetical joint proceeds that could arise in the first stage of the experiment.
These judgments allow us to examine the magnitude of the self-serving bias by the parties
in the experiment (winners and losers) and to obtain impartial judgments about whether and
how history should play a role in the situation created by the experiment.

<h>GENERAL CONSIDERATIONS OF THE BARGAINING EXPERIMENT</h>
---------------------------------------------------

In stage one of the bargaining experiment, we manipulated pairs’ histories by means of a
random allocation of proceeds generated in a real-effort task. In the shared history
condition, one single coin flip for each pair of subjects determined which of the two
individuals received remuneration for the task. Negotiators’ outcomes were therefore
interdependent, as only one party (the winner) received his/her stage one earnings, while
the other (the loser) did not get paid for completing the task. As a result of this stage
one manipulation regime, we solely obtained shared asymmetric (winner-loser) history pairs
in the shared asymmetric history condition. In the independent history condition, one coin
was flipped for each player, which determined whether the player received his/her stage
one earnings (and became a winner or loser). Depending on the outcomes of these coin
flips, we realized the following three different types of pairs in the independent history
condition: both players are winners, both players are losers, or one player is a winner
and one other the loser. Only the latter group, consisting of a winner and a loser, is
comparable in terms of material outcomes to pairs in the shared asymmetric history
condition. The two independent symmetric history conditions, consisting of two winners or
two losers, are uninformative for testing our hypothesis and are not included in the
section on testing predictions, although we do report bargaining outcomes in those
conditions. In a similar vein, although we also elicited fair divisions of joint proceeds
from judges for both types of independent symmetric history pairs (two winners or two
losers), we do not investigate these divisions in the hypothesis testing section. In stage
two, players completed a ten-item knowledge quiz remunerated in a piece-rate fashion. For
a similar approach see, e.g., Ball et al. (2001), Clark (1998), Gächter and Riedl (2006),
and Hoffman et al. (1994). The earnings of both players were pooled, and they then
negotiated over how to divide the pooled amount. The purpose of the real-effort tasks in
both stages of the experiment was to create a sense of entitlement on the part of the
subjects (Birkeland, 2013; Cherry et al., 2002). This had particular significance in stage
two, because we expected that knowing one's own and one's bargaining partner's individual
contributions to the joint proceeds would reduce the tendency of equal-split claims and
make splitting in proportion to each player's contribution a salient fair division (e.g.,
Gächter and Riedl (2006) and Ochs and Roth (1989)). This design feature also allows us to
define compensation. By compensation we mean giving to the loser beyond his/her
contribution to the stage two pooled earnings – i.e., compensating the loser at the
winner's expense. After both subjects in a pair finished working on the knowledge quiz,
they learned their own and their bargaining partner's individual earnings and the pooled
earnings. Then, they bargained over how to split their pooled earnings. Before the
negotiation began, players stated their beliefs about their own fair share of the earnings
expressed in Hungarian Forints (i.e., HUF). Subjects were not asked what they personally
viewed as a fair share, which we could not have elicited in an incentive-compatible
fashion, but instead were asked to predict the judgments of the impartial (in the sense of
not having a stake in the negotiation) judges whose judgments about a fair division had
already been elicited via the aforementioned preliminary survey administered. Subjects in
the bargaining experiment were then rewarded based on how close their predictions came to
the actual judgments of the impartial judges. This procedure is similar to that used in
prior research on self-serving assessments of fairness (e.g., Babcock et al. 1995, Gächter
and Riedl 2005).

<h>PREDICTIONS</h>
-----------

Our key behavioral prediction is that impasse will be more likely to occur in the shared
than in the independent asymmetric history condition. We anticipated that negotiators in
the shared asymmetric history condition would form divergent, settlement-hindering beliefs
about the fair settlement, while these beliefs would be more similar between negotiators
in the independent asymmetric history condition, which would facilitate settlement. More
specifically, we predicted that losers in the shared asymmetric history condition would
perceive a larger amount of compensation as fair than losers in the independent asymmetric
history condition or winners in any condition. Relatedly, we predicted that losers in the
shared asymmetric history condition would believe that they were entitled to compensation
relative to the proportion-to-input settlement, while winners would believe that
compensation was not called for. We also expected that impartial judges would perceive
compensation as fair for losers in both asymmetric history conditions, but that this would
be greater for losers in the shared than in the independent asymmetric history conditions.
We had no specific predictions about how much players’ and judges’ views of fair
compensation would overlap, nor about whether winners’ or losers’ perspectives would
deviate more from those of the unbiased judges.

<h>METHODS</h>
-------

The two-stage bargaining experiment was programmed in oTree (Chen et al., 2016) and
conducted in twenty-eight sessions. Each session lasted approximately fifteen minutes, and
participants received a 300 HUF show-up fee.1 Experimental screenshots in the original
language and their English translations can be found in Appendix A.

<hs>  Procedure</hs>
  ~~~~~~~~~

Subjects were recruited from Corvinus University of Budapest, Hungary. After arriving at
the lab facilities at the university, they read and signed the informed consent form and
were seated at one computer arranged so that subjects could not see others’ screens.
Assistants welcomed the subjects and informed them that they could discontinue the
experiment at any point, in which case they would only be paid their show-up fee. Subjects
were also informed that if they had any questions, they should raise their hand and
address them to the experimenter privately. Then, they clicked on a link which started the
experiment. In the first stage of the experiment, paired subjects (henceforth, players)
were randomly assigned to either the shared or the independent history pair-level
condition. After answering basic demographic questions, they were given a real-effort task
entailing labeling five simple images. For example, if an image of a spoon was presented,
they had to type the word “spoon.” Players in both pair-level conditions were truthfully
informed before they began the image-labeling task that, after they labeled all five
images, one image would be randomly selected for each player in a pair. If both parties
within a pair correctly typed in the name of this image, they both individually earn 1500
HUF. Pairs in which at least one party failed at successfully completing the image-
labeling task stopped the experiment after this stage and were only paid a show-up fee.
Players were also told that, upon successfully completing the image-labeling task, a
random device would decide whether they would be paid their 1500 HUF remuneration. At this
point, they were only told about these earnings and they were actually paid out at the end
of the experiment (this procedure was truthfully described in detail to the players). To
establish the shared history manipulation in the shared history condition, one coin was
flipped for each pair. That is, players’ outcomes were interdependent since only one of
them could in fact receive her/his 1500 HUF earnings for the image-labeling task. The
player favored by the coin flip (i.e., winner) received his 1500 HUF earnings, whereas the
player not favored by the coin flip (i.e., loser) did not receive his earnings of 1500 HUF
for completing the image-labeling task, but instead received 0 HUF. To establish the
independent history manipulation in the independent history conditions, one coin was
flipped individually for each player in the pair. That is, two coins were flipped
simultaneously for each pair creating independence between the players’ outcomes. The
outcomes of these two coin flips individually and independently determined for each player
whether s/he in fact receives the 1500 HUF earnings from the image-labeling task – i.e.,
was a winner or a loser. The outcomes of these two coin flips created three different
independent history conditions. When one of the two coin flips favored one player (i.e.,
winner) but the other coin flip did not favor the other player (i.e., loser), as in the
independent asymmetric history condition, the winner received his/her 1500 HUF earnings
while the loser did not receive her/his 1500 HUF earnings. When the two coin flips favored
both players, as in the independent symmetric history winner-winner condition, they both
received their 1500 HUF earnings for completing the image-labeling task. When the two coin
flips favored neither party, as in the independent symmetric history loser-loser
condition, neither player received his/her 1500 HUF earnings for completing the image-
labeling task, and instead, they each received 0 HUF. At the end of stage one, the coins
were flipped and players learned the outcomes of the coin flips corresponding to their and
their partner's earnings. That is, players in all conditions were not only informed about
whether they received their 1500 HUF but also whether their partner received his/her 1500
HUF for completing the image-labeling task. In the second stage, player pairings were kept
the same as in stage one. At the beginning of this stage, players were reminded about
their own and their partner's stage one history – i.e., the partner's coin flip outcome
and earnings – and then were given instructions for stage two. Next, they individually
worked on the same ten-item trivia quiz for which each correct answer yielded 150 HUF for
each of them. Once quizzes were completed, they learned their own score on the quiz (i.e.,
how many correct answers they gave), their individual earnings in HUF, their partner's
quiz correct score and earnings in HUF and their joint quiz earnings in HUF. As a proxy
for their beliefs about their unbiased fair share, players then provided their best guess
(expressed in HUF) of the mean judgement of five impartial judges of the fair division of
their pooled stage two trivia quiz proceeds (see Appendix A for the exact wording). This
belief elicitation procedure was incentivized as follows. Players were told, truthfully,
that five neutral judges, who had been informed about both partners’ stage one history and
both parties’ individual contribution to the joint stage two quiz earnings, had judged
fair splits of their joint proceeds. Each player who answered within 10% of the mean of
these judgments received an extra 300 HUF. To avoid wealth effects, however, they only
learned whether they had earned this bonus at the end of the experiment. The beliefs were
then compared to results from a preliminary judge survey. In this preliminary judge
survey, we elicited five fair divisions for each one of every possible combination of
pooled trivia earnings between players in all four pair-level conditions. Each combination
was judged by five different judges, and these judgments were averaged, creating a large
table of means that was used in the main experiment. Appendix A provides a detailed
description of this preliminary judge survey in which fully informed neutral judges
proposed fair splits between players. After participants stated their beliefs about their
fair share (their prediction of the judges), they entered the bargaining phase, in which
they were given three rounds to agree on how to divide their joint quiz proceeds.
Negotiators simultaneously submitted their offers (i.e., how much they would like to take
for themselves) and then learned how much their bargaining partner claimed. If offers
summed up to the joint proceeds, then they agreed and received as much as they claimed. If
their offers summed to less than the joint proceeds, they received their claims and the
leftover funds were equally split between them. If offers summed to more than joint
proceeds, then they entered the next round. If they failed to agree in the third round,
the amount to be divided shrank by 20% and was randomly (with every division equally
likely) distributed between parties. Once players were done with the bargaining (i.e.,
they either settled or reached impasse), they learned how much they had earned in the
bargaining phase. Next, they responded to a seven-item survey presented in two clusters.
In the first cluster, which was two items, one item asked them how much they agree with
the statement that it is fair to compensate from the joint quiz earnings the party who did
not get paid for the image-labeling task. The other item asked them how much they agree
with the statement that how much someone earned from the image-labeling task should have a
bearing on the fair division of the joint quiz earnings. In the second cluster, which was
five items, players answered questions about their satisfaction with and feelings about
their bargaining outcomes. Finally, they learned how much they earned in the experiment in
total and were paid.

<hs>  Sample</hs>
  ~~~~~~

Subjects in the bargaining experiment and respondents to the judge survey were recruited
from Corvinus University of Budapest, Hungary, spanning a wide variety of study fields
such as marketing, sociology, international relations, economics, applied economics, and
business administration. Those who participated in the preliminary judge survey were not
allowed to participate in the bargaining experiment. There were no other exclusion
criteria for participation. Five-hundred twenty-two subjects (261 pairs) participated in
the bargaining experiment, but eight players failed to pass the image-labeling task (by
chance, all in the independent symmetric history condition). The final sample consisted of
514 players (257 pairs), 91 pairs in the shared asymmetric history, 75 pairs in the
independent asymmetric history, 45 pairs in the independent symmetric history loser-loser,
and 46 pairs in the independent symmetric history winner-winner condition. Additionally, a
total of 109 participants completed the preliminary judge survey.2 Specifically, 23
individuals made judgments about earning combinations occurring in the shared asymmetric
history condition, 26 about the independent asymmetric history conditions, 32 about the
independent symmetric history loser-loser, and 28 about the independent symmetric history
winner–winner conditions. Comparing the demographics of the shared and independent history
conditions, the only difference between the groups was that winners in the shared
asymmetric history condition are younger (Mean (SD) = 20.75 (1.51)) than winners in the
independent history treatment (Mean (SD) = 22.17 (4.59)), W(1, 87) = 6.66, p ≤ 0.05.
Comparing survey participants’ (judges’) and players’ demographic characteristics, the
mean age in years is significantly higher among judges (Mean (SD) = 23.07 (4.25)) than
players (Mean (SD) = 21.39 (2.84)), F(1, 617) = 25.66, p ≤ 0.001. In other aspects, there
are no differences between players’ and judges’ demographic characteristics. Detailed
demographics are presented in Appendix Table B1 for players and in Tables B2 and B3 for
judges.

<h>RESULTS</h>
-------

First, we present descriptive results from all four pair-level treatments. Then, we
continue with testing predictions on the restricted sample of shared asymmetric history
and independent asymmetric history treatments.

<hs>  Descriptive results</hs>
  ~~~~~~~~~~~~~~~~~~~

The upper panel of Table 1 presents descriptive results of players in the bargaining
experiment. From the first row one can see, consistent with the random assignment to
winning or losing in stage one and to one of the history conditions, that there is no
significant difference across individual-level conditions in players’ contributions to the
stage two pooled quiz earnings. Players in a pair contributed, on average, 50% of the to-
be-divided joint earnings, suggesting that the stage one manipulation did not impact their
stage two effort levels. The marginal (i.e., overall, across treatments) mean (SD) is
1044.75 (223.54) HUF, which corresponds to a mean (SD) of 6.96 (1.49) correctly answered
quiz questions. Note, that there is also no difference in the stage two pooled earnings
between the four pair-level treatments, F(3, 253) = 0.29, ns; the mean (SD) for all
players is 2089.49 (323.77) HUF. The mean experimental earnings in HUF (excluding the
show-up fee) differs across individual-level treatments, mostly due to the stage one
loser-winner manipulation. In general, winners earned more than losers in the experiment.
Players’ beliefs about their fair share expressed proportional to their stage two quiz
earnings (i.e., how much the player stated that s/he should get in HUF according to
impartial judges divided by her/his individual stage two quiz earnings in HUF) are
presented in the second row of Table 1. Results show that losers in both asymmetric
history conditions believe they are entitled to a greater share than their winner partners
believe they are entitled to. Losers in the shared asymmetric history condition believe
they are entitled to a greater share than losers in the independent asymmetric history
condition, F(1, 164) = 21.61, p ≤ 0.001. Losers in both asymmetric history conditions
believe that they are entitled to more than their contributions (their 95% CIs are above
1), whereas winners, on average, believe that they are entitled to no more than their
contribution (95% CIs include 1). The lower panel of Table 1 presents judges’ views about
players’ fair share expressed as a proportion of stage two joint earnings. Two findings
emerge here. First, in both asymmetric history conditions judges think it is fair to give
a larger share to losers than to winners. Second, they believe that losers in both
asymmetric history conditions are entitled to more than their contributions in the second
stage, as the 95% CIs are above 1. This amount is, however, larger for losers in the
shared than in the independent asymmetric history treatment, W(1, 24) = 49.83, p ≤ 0.001.
Although judges’ views of fairness in the two symmetric conditions were mainly solicited
to determine fair shares for subjects in these conditions, these judgments do address the
question of whether judges believed that, absent asymmetries, players should be paid in
proportion to their earnings. The answer is that they do hold this view: on average,
judges believe that losers and winners in the two symmetric history treatments are
entitled to their contributions. When comparing the 95% CIs of the means of players’
beliefs (second row of first panel) and judges’ views (first row of second panel) about
players’ fair shares, we observe that these views overlap between players and judges in
every individual cell except for winners in the shared asymmetric history treatments.
These winners believe that fairness does not dictate granting losers beyond their
contribution to the stage two joint earnings; but judges do believe that such additional
compensation was fair. Further details about stage two joint quiz earnings in HUF,
players’ stage two quiz and experimental earnings in HUF, and judges’ views in HUF are
presented in Table B4 in Appendix B. The main results of the experiment are presented in
Fig. 1. Looking first at settlement versus non-settlement (right-hand bar in each figure),
the distribution of impasse differs between the four pair-level treatments, χ2(3, Npair =
257) = 14.68, p ≤ 0.01 in the predicted fashion. Specifically, impasse is more likely in
the shared asymmetric history treatment (22%) than in the independent asymmetric history
treatment, where it was only 7%, χ2(1, Npair = 166) = 7.53, p ≤ 0.01. Comparison of the
independent asymmetric history treatment to those in the two symmetric history treatments
shows that impasse rates are similar across these three treatments, χ2(2, Npair = 166) =
0.32, ns. However, the pattern of settlement does differ between these three treatments.
Specifically, pairs seemed to settle more quickly in the two independent symmetric history
treatments than in the independent asymmetric condition. Finally, we find no difference in
the likelihood of impasse within the two independent symmetric treatments, χ2(1, Npair =
91) = 0.24, ns.

<hs>  Tests of predictions involving fairness perceptions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

To specifically test our predictions about the differential impact of shared and
independent histories on asymmetric history pairs, we restrict the sample to the shared
and independent asymmetric history treatments (Nindividual = 332). To simplify
comprehension and analysis, we express players’ beliefs and judges’ views about the fair
solution in terms of loser's share, which facilitates interpreting the results from the
perspective of compensation given to loser. The loser's share is defined as the difference
between the stated beliefs (players’ or judges’) about the amount the loser should receive
and the amount contributed by the loser, scaled by the joint stage two quiz earnings.
Loser's share = (amount in HUF loser should get – amount in HUF loser contributed)/pooled
quiz earnings in HUF This form is commensurable within and between pairs and between
players and judges. Additionally, it highlights whether the loser's share that is
perceived as fair is more than his/her contribution to the pooled stage two quiz earnings,
indicating the presence of compensation for the loser at the winner's expense. Using this
formula, we first calculate, and present in Fig. 2, the mean players’ belief about the
loser's fair share in each individual-level condition. Three important findings emerge
from the 95% CIs of the means. First, winners in the shared and independent asymmetric
history conditions believe that splitting according to contribution is the fair
settlement, as the 95% CIs of mean beliefs include zero. Second, losers in both pair-level
conditions believe that the fair settlement includes giving more to losers than their
contribution, as the 95% CIs include only positive numbers. In other words, losers in both
conditions believe that their fair share includes compensation from their winner partners.
Third, losers in the shared asymmetric history condition believe that a greater share is
fair than losers in the independent condition or winners in any condition. The statistical
significance of the third finding is confirmed by the history-by-loser interaction in
Model I of Table 2, which regresses players’ beliefs about the loser’s fair share on
history (shared asymmetric = 1 vs. independent asymmetric = 0) and role (loser = 1 vs.
winner = 0). The psychology suggested by this pattern receives further support from
responses to the second item from the short survey administered at the end of the
experiment: “How much someone earned from the image-labeling task has a bearing on what is
the fair division of the joint earnings.” Losers (Mean (SD) = 2.92 (0.92)) in the shared
asymmetric history condition agree more than their winner partners (Mean (SD) = 2.56
(0.90)) with this statement, F(1, 180) = 7.23, p ≤ 0.01. They also agree more than losers
in the independent asymmetric history condition (Mean (SD) = 2.55 (0.79)), F(1, 164) =
7.76, p ≤ 0.01. At the same time, there is no loser and winner difference within the
independent history condition. These responses should be treated with caution, however,
since they were not incentivized and could just be justifications of behavior displayed in
the experiment rather than true motives. Next, we calculate the difference between
negotiators’ beliefs about the loser's fair share (i.e., loser's–winner's beliefs about
loser's fair share) and plot the distributions in the two pair-level asymmetric history
conditions in Fig. 3. Following Gächter and Riedl (2005), we refer to this difference as
‘tension’ between the individuals. As evident from the figure, the distribution of tension
differs between the two conditions, Kolmogorov–Smirnov Z = 2.55, p ≤ 0.001. Most notably,
the bulk of the tension is centered around zero in the independent asymmetric history
condition, while it is concentrated in the positive domain in the shared asymmetric
history condition. Mean tension is greater among pairs in the shared asymmetric history (M
(SD) = 0.16 (0.16), 95% CI [0.13, 0.19]) than in the independent symmetric history
condition (M (SD) = 0.06 (0.17), 95% CI [0.02, 0.10]), F(1, 164) = 14.33, p ≤ 0.001. In
fact, as one can see from the 95% CIs, tension is greater than zero in both pair-level
treatments, indicating that players in both treatments hold incompatible beliefs about the
loser's fair share, though beliefs are more discordant between players in the shared than
in the independent asymmetric history condition. We perform a series of binary logistic
regressions to test the effect of shared history on impasse (Model I), and then we add
tension (Model II), see Table 3 for a summary of results. From Model I, we learn that
impasse is approximately four times more likely in the shared than in the independent
asymmetric history condition. Adding tension, in Model II, we find that an increase in
tension from its mean value (0.16) to its maximum (0.60) in the shared asymmetric history
condition results in a change in expected probability of impasse from 20.5% to 56.3%. The
equivalent increase from the mean (0.06) to the maximum (0.58) in observed tension in the
independent asymmetric history condition also results in an increase in the expected
probability of impasse, but a smaller one, from 5.3% to 32.6%. In Table B5 in Appendix B
we also show that the effects of history and tension are robust after controlling for the
difference between players’ age and effort levels (i.e., stage two quiz earnings) within a
pair and the gender composition of a pair. One may wonder if there is a difference between
settled and not-settled pairs in the shared asymmetric history condition with respect to
their stage two quiz effort levels. Restricting the sample to this condition (Npair = 91),
we find no difference between non-settled and settled pairs in this respect. The mean (SD)
and 95% CI of quiz correct score signed difference for settled-pairs are −0.03 (0.17)
[−0.07, 0.01] and for non-settled pairs are 0.03 (0.19) [−0.05, 0.13], F(1, 89) = 1.89,
ns. Similarly, the distribution of quiz correct score signed difference does not differ
between settled and non-settled pairs in the shared history condition, Kolmogorov–Smirnov
Z = 0.83, ns. Results of a causal mediation analysis using the method of Imai et al.
(2010a, 2010b) help to reveal the mechanism via which shared history affects impasse. On
average, shared asymmetric history increases the probability of impasse by 0.15, and we
find that 28% of that total effect is due to history's positive effects on tension. In
other words, at least part of the reason that the shared asymmetric history increases
impasse is because it increases the divergence between players’ beliefs about the loser's
fair share.3 Next, we examine judges’ views about the loser's fair share. Recall that
judges' views are in reference to a pair and are from the preliminary survey of those
loser–winner quiz earnings combinations that occurred in the two asymmetric history
conditions of the bargaining experiment (23 in the shared and 26 in the independent
asymmetric history condition). The distribution of judges’ views in the two pair-level
treatments is plotted on Fig. 4, which reveals a difference between the two distributions,
Kolmogorov–Smirnov Z = 3.02, p ≤ 0.001. Perhaps the most striking result is that, while in
80% of the independent asymmetric history cases judges would not compensate losers beyond
their contribution to second stage joint earnings, in most of the cases in the shared
asymmetric history treatment judges would grant shares to losers that surpass their
contribution to the second stage task. In fact, on average, judges would grant 21% more to
losers in the shared than in the independent history condition. The mean (SD) and 95% CI
of loser's share is 0.23 (0.10) and [0.19, 0.27] in the shared and 0.02 (0.03) and [0.01,
0.04] in the independent history conditions, W(1, 26) = 95.24, p ≤ 0.001. Nonetheless,
from these 95% CIs we also see that judges do grant compensation to losers in both
conditions. Finally, we determine the difference between players’ and judges’ beliefs
about the loser's fair share (i.e., each player's stated beliefs minus the mean judges'
view for the corresponding joint earnings case) and regress these differences on history
(shared asymmetric = 1 vs. independent asymmetric = 0) and role (loser = 1 vs. winner =
0). As can be seen from the significant history by role interaction in Table 4, which is
evident also in Fig. 5, in absolute terms, winners’ beliefs in the shared asymmetric
history condition deviate the most from judges’ views in a way that benefits them (i.e.,
giving beyond their contribution to losers is unnecessary). Losers in this condition,
however, believe they should be entitled to slightly less than the amount that judges
believe is fair. The pattern is almost flipped for players in the independent asymmetric
history condition. On average, losers here believe that they are entitled to more than
judges would give them, while their winner partners formed concordant beliefs with the
judge view.

<h>DISCUSSION</h>
----------

We introduced two types of prior wealth asymmetry between bargainers and demonstrated that
when the asymmetry is due to negotiators’ shared history, it is more likely to cause
impasse than when it is due to negotiators’ independent history. This result is consistent
with key findings of Camerer and Loewenstein (1993) and Dezső et al. (2015) about the
pernicious potential of asymmetric history in negotiations. Though the conclusions of
these papers are similar to ours, in the former paper asymmetry was not experimentally
manipulated, whereas in the latter paper, asymmetry and interdependent history were not
disentangled. To remedy these issues, we experimentally manipulated asymmetry and isolated
the effect of asymmetry from interdependent history. We showed that it is not the
asymmetry per se but the allocation schema by which it occurs that leads to elevated rates
of impasse. The finding that sharedness and not asymmetry is the key issue between
negotiators is also supported by the lack of difference between the likelihood of
settlement between independent asymmetric and symmetric treatments. We argue, and
demonstrated empirically, that these stalemates are due, in large part, to negotiators’
divergent and self-serving beliefs about the fair settlement. Losers in both asymmetric
history conditions believed that they deserve more than their contribution from the joint
proceeds, indicating that they believed that the fair solution prescribes compensating
them for their prior loss. Nonetheless, losers with shared histories believed that they
were entitled to a greater share than losers with independent history. On the other hand,
winners with shared asymmetric history did not believe that the loser should get more than
his/her contribution, which caused a significant divergence between losers’ and winners’
beliefs about the fair settlement in the shared asymmetric history treatment. By contrast,
divergence between losers’ and winners’ beliefs about the loser's share were much smaller
in the independent asymmetric history treatments, even though winners here also did not
believe that giving to the loser beyond his/her contribution was necessary from the
vantage point of fairness. All in all, players in all conditions self-servingly selected
the fair solution that was the most beneficial for them, which led to a discordance
between them on the issue of compensating the loser. The divergence of these beliefs was,
however, smaller for pairs in the independent asymmetric history condition and hence,
hindered settlement to a lesser extent. This key role of beliefs confirms the speculations
of Camerer and Loewenstein (1993) and Dezső et al. (2015) about the self-serving potential
of asymmetric history, though beliefs about the fair settlement were not elicited in
either of these papers. The finding that negotiators’ relatively extreme perceptions of a
fair settlement drove impasse provides empirical support for the proposition of Birkeland
and Tungodden (2014) regarding principled disagreement. When bargainers arrive at the
negotiation with highly incompatible beliefs, they insist on them even at the cost of
reaching impasse. The results of the judge survey demonstrate that, from the vantage point
of a neutral judge, past outcomes do have implications for fairness in the present.
Redistribution is seen as fair when it involved parties sharing an asymmetric history, but
less so when they had independent histories. In other words, a winner who benefited at the
expense of a loser should compensate the loser with a greater amount than when the winner
did not benefit at the loser's expense, as in the independent history condition. All in
all, unbiased judges believe that fairness dictates compensation for those who received
the short end of the stick in a prior division. When we compared players’ beliefs about
the losers’ fair share to those of unbiased judges’, an interesting pattern emerged. On
the one hand, only independent history winners’ beliefs overlapped with the impartial fair
solution. Losers in this condition believed they were entitled to more than the judge's
judgments prescribed. On the other hand, shared asymmetric history winners’ views of fair
compensation to losers fell below the judges’ unbiased judgments of the losers’ fair
share, and, surprisingly, the losers also believed they were entitled to less than the
amount deemed fair by the judges.

<hs>  An alternative interpretation</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

A potential alternative interpretation of our key finding is that the shared asymmetric
history may have ignited a motivation to compete in losers when the playing field was
finally leveled. This interpretation does not seem incompatible with the one we propose;
it is an alternative, related mechanism that could produce a desire for compensation on
the part of the loser, with no commensurate willingness to provide such compensation on
the part of the winner. Note, however, that this interpretation would not predict the
difference in views on fairness that the self-serving interpretation of fairness account
predicts, and that we in fact found.

<h>CONCLUSIONS</h>
-----------

We believe that these and prior related results help to shed light on the prevalence of
conflict between parties with a shared, and almost inevitably asymmetric history, such as
business partners seeking a dissolution of the partnership, divorcing spouses, and
competing countries. Our experiment suggests that the effects of self-serving bias in
these situations will be worst when one party's history is less favorable than the
other's, and, more specifically, when one of those parties gained at the other party's
expense. Research on climate change negotiations reveals similar tendencies in countries’
argumentations on the burden of emissions’ reductions. Due to the complexity of this
issue, multiple fair solutions arise, each corresponding to different sharing rules and
different costs being imposed on countries (Kriss et al., 2011; Ringius et al., 2002). One
element of this complexity, which is self-servingly invoked, is the interpretation of the
significance of historical emissions for the fair sharing of current costs (Cazorla and
Toman, 2000). Decades of unrestricted greenhouse gas emissions strongly contributed to the
economic prosperity of many developed countries. Current developing countries would now
like their turn at industrialization, and restricting emissions seriously constrains their
economic growth prospects. Due to their asymmetric histories of pollution and economic
growth, rich and poor countries self-servingly invoke or ignore emission history. Poorer
countries argue that richer countries must take a lead in accepting greater abatement
costs because they are more responsible for the current high level of greenhouse gases and
they have already benefited from polluting activities (Lange et al., 2010). By contrast,
richer countries claim that the fair solution is “cleaning the slate” and splitting the
burdens, independent of emission history. Given the subtlety of the shared/independent
manipulation, it is remarkable that it had such a strong effect. After all, the two people
were paired together, and could have viewed the gain of one and loss of the other as
relevant. In the real world, such asymmetric independent histories might have a smaller
impact. A potential threat, however, is that leaders will use the effects revealed in the
experiment to manipulate constituencies. They may attempt to instill in people who are in
inferior wealth positions the view that their misfortune stems from a shared asymmetric
history with other groups, such as immigrants. Creating such a narrative, the current
research suggests, may instill and invoke self-serving interpretations among those feeling
they are in a disadvantaged position. The unfortunate consequence is, as demonstrated in
our experiment, a further discord between these people and, perhaps, a breeding ground for
a lingering desire to even the score with those who previously benefited. There is,
however, a small silver lining to our research. An important property of self-serving
perspectives on fairness is that people generally believe that impartial judges will share
their own biased views. Since both parties genuinely believe that their perspective on
fairness will be shared, they should both be open to arbitration. In conclusion, a shared,
asymmetric history can lead to discord between parties, due to individuals’ self-serving
interpretations of the implication of history. Whether one adopts the view “let bygones be
bygones,” or sees the past as relevant to the future, depends on how one fared in the
past, and on the degree to which the other party was responsible. Disputes between
overworked employees are examples of relatively innocuous consequences of self-serving
invocations of history, but these are also evident in high-stakes situations, such as
disputes on fulfilling refugee quotas in Europe or bearing the costs of reducing
greenhouse gas emissions all over the world. Divergent, self-serving invocations of
history hamper agreement on how to share sacrifices for the greater good and may also
further undermine international cooperation on issues from which we would all gain from
settling. Identifying the motivations ignited after being wronged is an important link to
understanding how interacting parties’ shared and asymmetric history could spill over into
subsequent disputes. These conflicts may range from the mundane to crucial international
debates, including the creation and maintenance of well-balanced power structures and,
most importantly, saving our planet.


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<ART>Social preferences are stable over long periods of time
=======================================================

Authors: Fredrik Carlsson, Olof Johansson-Stenman, Pham Khanh Nam
DOI: 10.1016/j.jpubeco.2014.05.009
Year: 2014  |  Pages: 104-114
ASJC codes: 2002, 2003
Keywords: Natural field experiment, Preference stability, Social preferences, Voluntary contributions

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We measure people's pro-social behavior, in terms of voluntary money and labor contributions to an archetypical public good, a bridge, and in terms of voluntary money contributions in a public good game, using the same non-student sample in rural Vietnam at four different points in time from 2005 to 2011. Two of the observed events are actual voluntary contributions (one in terms of money and one in terms of labor), one is from a natural field experiment, and one is from an artefactual field experiment. Despite large contextual variations, we find a strong positive and statistically significant correlation between voluntary contributions, whether correcting for other covariates or not. This suggests that pro-social preferences are fairly stable over long periods of time and contexts. © 2014.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The present paper investigates the stability of social preferences by utilizing unique
data on people's voluntary contributions to an archetypical public good, a bridge, and
contributions in a public good game. The analysis is based on two observations of
voluntary contributions, one natural field experiment on contributions to a real bridge in
rural Vietnam, and one artefactual field experiment on contributions in a public good
experiment, conducted from 2005 to 2011 and using the same sample consisting of all (about
200) households in a village in rural Vietnam. Thus, we obtain repeated information on
people's pro-social preferences over a long period of time. An overwhelming amount of
psychological and behavioral economics research shows that the Homo Economicus
characterization of human behavior, in terms of complete selfishness in a narrow material
sense, is often importantly wrong; human behavior is in part pro-social. At the same time,
a large heterogeneity in pro-social behavior is typically found. Several studies have
consequently attempted to categorize people, based on their experimentally observed
behavior, in terms of different types of social preferences, e.g., as free riders,
conditional cooperators, and unconditional cooperators (Fischbacher et al., 2001); as
selfish versus inequity-averse individuals (Fehr and Schmidt, 1999); and as non-sharers,
reluctant sharers, and willing sharers (Lazear et al., 2012). Yet, from these studies one
cannot conclude that people are inherently of different types. An alternative explanation
is that people simply act differently at different points in time, and that people's
degrees of cooperativeness, or non-selfishness, are approximately constant on average.
Indeed, that people's pro-social actions vary over time is obvious since most of us
sometimes contribute to a certain charity and sometimes not. Yet, how much of the observed
heterogeneity in social preferences that can be explained by within-people variations is
not clear, nor is it clear whether it is significantly more likely that an individual who
acted cooperatively at one point in time is more likely to act cooperatively in a similar
task several years later. Moreover, even if people are of different types with respect to
pro-social preferences, it is an important research issue to find out whether these types
are stable over longer periods of time. The present paper is, to our knowledge, the first
in economics to systematically investigate whether pro-social preferences, manifested in
terms of cooperative behavior, are fairly stable over several years. In contrast, the
extent to which preferences, and in particular social preferences, are stable over a short
period of time, and also across decision environments, has been studied in a number of
papers with different methods. Some studies have looked at the differences in pro-social
behavior between similar experiments conducted at different points in time. For example,
Brosig et al. (2007) conducted dictator and public good games with the same subjects at
several points in time over the course of one week. Other-regarding behavior was found to
decrease over time, and in the final experiments the subjects' behavior was close to that
predicted by conventional economic theory. Subjects who behaved selfishly were found to be
the only ones who behaved stably over time. This pattern is similar to the one typically
obtained with repeated public good games.3 Volk et al. (2012) had subjects participate in
a series of three identically designed public good experiments over a period of five
months. At the aggregate level, cooperation preferences were stable. However, at the
individual level there was considerable variation. Classifying subjects into three
categories – conditional cooperators, free riders, and others – it was found that half of
the subjects remained in the same category in all three experiments. Other studies have
looked at differences in pro-social behavior between different experiments (with the same
subjects). Blanco et al. (2011) ran four different experimental games: dictator,
ultimatum, sequential-move prisoners' dilemma, and public good games, and tested whether
the Fehr and Schmidt (1999) inequity aversion model can explain the results. They found
that the model could explain the results reasonably well at the aggregate level, but that
it performs considerably less well at the individual level. De Oliveira et al. (2012)
found that preferences for contributing to public goods are positively related across
different experimental decision contexts, and also positively related to self-reported
donations and volunteering outside the laboratory. Yet other studies have compared
contributions in the lab and in the field. Benz and Meier (2008) conducted a dictator game
with two social funds as external recipients and found a positive, albeit relatively weak,
correlation between subjects' behavior in a lab experiment and actual charitable giving.
Laury and Taylor (2008) found mixed evidence regarding the correlation between non-selfish
behavior in laboratory experiments and contribution to a charitable organization. While
they found that some measures of altruistic behavior in the lab could be predictive of
contributions to the charity, the relationships were generally weak, and some measures of
altruism were even negatively correlated with contribution to the charity. Based on a
trust game in Peru, Karlan (2005) found that subjects identified as trustworthy, i.e.,
receivers who returned a relatively large share of what they received from the senders,
tend to repay their microcredit loans to a larger extent than those who were not
identified as trustworthy in the experiment. No significant correlation between those
identified as trusting, i.e., senders who sent a relatively large share to the receivers,
and repayment of the loans was obtained. Fehr and Leibbrandt (2011) found that fishermen
in Brazil who are more cooperative and patient in lab experiments are also less likely to
exploit the common pool resource in the sense that they use shrimp traps with bigger holes
(where small shrimp can escape) and fishnets with larger mesh sizes (where only bigger
fish are caught). Algan et al. (2013) combine an online experiment with field contribution
data for 850 Wikipedia contributors. They found that actual contributions to Wikipedia are
strongly related to levels of reciprocity as revealed by both a conditional public good
game and trust game. However, they found only weak links with altruism as revealed by
dictator game contributions. Cesarini et al. (2009) used a different approach based on
twin studies combined with modified dictator experiments to determine the extent to which
giving is heritable. Their best point estimate suggests that genes explain about 20% of
the variation in behavior among subjects and hence that social preferences, as manifested
in giving behavior in dictator experiments, are in part explained genetically. Yet, this
is not necessarily a good measure of the degree to which social preferences are constant
over time. First, a certain genetic set-up may in principle induce variation in behavior
over time. Second, there are many environmental factors that may work in the direction of
stabilizing social preferences, e.g., the development of close relations and social
norms.4 In summary, most of the studies discussed above point in the direction that social
preferences are partly stable over different domains and over time, although the extent of
the stability varies between studies to a rather large extent. The main contribution of
the present paper is that it investigates the stability of social preferences over long
periods of time, where also the contexts differ; we observe behavior in four different
periods: in 2005, 2009, 2010, and 2011. As a result of the relatively long time between
our events, we argue that we can also more or less rule out the potentially confounding
effects of compensatory behavior due to moral licensing and moral cleansing.5 The rest of
the paper is organized as follows. Section 2 describes the four observations of voluntary
contribution and the design of the two experiments, and provides the corresponding
background statistics. Section 3 presents the results. We find strong positive and
statistically significant correlations between voluntary contributions in these events,
whether correcting for other covariates or not, suggesting that pro-social preferences
seem to be quite stable over long periods of time.6 Section 4 concludes the paper.

<h>THE FOUR OBSERVED EVENTS OF PRO-SOCIAL BEHAVIOR</h>
-----------------------------------------------

We use observations of subjects' pro-social behavior in four related events in 2005, 2009,
2010, and 2011, i.e., implying rather long time periods between events and a total study
period of about six years. Two of the events (in 2005 and 2010) are naturally occurring
ones where we simply observed the behavior, and the other two (in 2009 and 2011) were
designed by the authors. Two of the events (in 2005 and 2009) concern monetary
contributions to a local public good in terms of the construction of a crucial bridge in
the middle of the village, one of the events (in 2010) concerns labor contributions to
construction of the same bridge, while the last experiment (in 2011) was a public good
experiment not related to the bridge at all. The first three observations, i.e., in 2005,
2009, and 2010, deal with a real event related to the construction of a bridge. The event
in 2009 can moreover be classified as a natural field experiment, whereas the last
experiment is an artefactual field experiment, i.e., a lab experiment conducted in the
field with a non-student sample. All four events focus on voluntary contribution
mechanisms, and although there are a number of contextual differences, in each instance we
observe the behavior of the same (approximately 200) subjects, representing all households
in the village. The events were undertaken in the Giong Trom hamlet,7 in the Mekong river
delta of Vietnam, where about 200 households live and use the bridge (if/when it is in
sufficiently good shape). Most households in the hamlet are engaged in rice cultivating
activities.8 The hamlet suffers from a problem that is common in the Mekong river delta:
lack of basic infrastructures such as rural roads, bridges, and irrigation canals. The
government only provides larger public goods such as roads between villages, whereas
small-scale infrastructures within a hamlet are considered to be the responsibility of the
hamlet.

<hs>  The bridge and the voluntary contributions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The bridge is important for the village because villagers use it to go to the rice fields,
to the market, to school, and to visit friends, given that the bridge is in sufficiently
good condition. If they do not use the bridge, they have to choose one of two other
routes, each located parallel to and about 1200 m from the bridge's pathway; see the map
in Fig. 1. There are people living on both sides of the canal, and there is also important
infrastructure on both sides of the canal. For example, the main market is located on the
north side of the canal, while the school is located on the south side. For all but a few
households, the travel distance to reach the destinations on the other side is
considerably longer if they cannot use the bridge. The first three observations of pro-
social behavior, to be described next, concern funding of a bridge for the hamlet.

<hs>  The 2005 event</hs>
  ~~~~~~~~~~~~~~

In the first event in 2005, the hamlet council had decided to try to build a bridge, which
was to be funded by voluntary contributions. A group of three delegated individuals
visited every household in the hamlet to present the plan to build the bridge and to ask
for voluntary contributions. Probably in order to persuade villagers and increase
contributions, the delegates showed a list of names, contribution amounts, and signatures
of those who had already contributed. The hamlet council did not set an upper contribution
limit, and the highest contributed amount was 300,000 dong.9 Since the total contribution
was not sufficient to build a concrete bridge, the hamlet council decided to build a
wooden bridge. Yet, the bridge became degraded relatively quickly, and in 2009 it looked
like in the picture in Fig. 2 and could obviously not be used for tractors and motorbikes.
The full list of contribution amounts from each household was kept by the hamlet council
and made available to the authors of this paper.

<hs>  The 2009 experiment</hs>
  ~~~~~~~~~~~~~~~~~~~

In collaboration with an NGO, we conducted a field experiment using a threshold public
good game that concerned the funding of a new bridge for the hamlet in 2009. Fifteen
experimenters were recruited via advertisements and a careful selection procedure at the
University of Economics Ho Chi Minh City. The selected experimenters received extensive
training and spent nearly one week practicing the experiment in role-play pairs and for
pilot interviews with farmers. Moreover, the selected experimenters also had experience
from similar fieldwork in a neighboring rural area. A list of likely questions and answers
related to the project was provided and the experimenters were repeatedly told about the
importance of using the exact wordings prescribed in the script. For a detailed
description of the experiment and the results, see Carlsson et al. (2013). The main
objective of the experiment was to investigate the role of social influence for voluntary
contributions to public goods. We devised a threshold public good game, in which each of
the 200 households received a 400,000 dong endowment from the NGO and had the option to
either keep the money or contribute some or everything to the funding of the bridge. The
threshold level was set at 40 million dong, meaning that if all villagers together would
contribute at least 40 million dong, the bridge would be built; otherwise it would not.
The threshold was explained as follows: The concrete bridge will be established if all
families together contribute at least 40 million dong. This means that if the total
contribution is equal to or above 40 million dong, the project will use these 40 million
dong, add more funding in order to meet the costs of the bridge, and take the
responsibility to build the bridge. If the total amount of money collected exceeds 40
million dong, the excess amount will be returned to your family according to the
proportion you contributed. If the families are unable to contribute a total of 40 million
dong, your contribution will be returned to you, and the concrete bridge will not be
built. The experiment involved five randomly distributed treatments as follows: 1.
Baseline case with no reference contribution level and no default option. 2. High
reference contribution level (300,000 dong) and no default option. 3. Low reference
contribution level (100,000 dong) and no default option. 4. No reference contribution
level and a default option at zero contribution, and 5. No reference contribution level
and a default option at full contribution (400,000 dong) of the endowment. The reference
contribution levels were conducted by providing the subjects with information about a
typical previous contribution of others. These numbers, in turn, were obtained from an
initial treatment where we did not tell the subjects anything about others' contributions.
The default options were conducted using a metal card with 9 different contribution
levels. A magnetic token was initially put at the 0 dong level or at the 400,000 dong
level. The subjects were then asked to move the token to the amount that they wanted to
contribute to the public good. In all treatments, the contributions were anonymous to
everybody except the solicitors, i.e., the contributions were not revealed to any parties.
Since the households contributed enough to reach the threshold, the new bridge was built
in early 2010; see the picture in Fig. 3.

<hs>  The 2010 event</hs>
  ~~~~~~~~~~~~~~

During the planning of the construction, we had a meeting with the head of the hamlet and
representatives from the farmers' association. At the meeting, we were informed that they
planned to ask the villagers to contribute labor to connect the road with the new bridge.
We took this opportunity to collect another naturally occurring contribution data set. As
the construction work required joint efforts in a short period of time, three and a half
day were scheduled for the joint work. Two persons from the hamlet council visited the
households in the hamlet to invite villagers to contribute labor. Hence, an important
difference compared with the previous two events is that instead of being asked for
monetary contributions, they were asked for labor contributions. Since some households
were not expected to be able to contribute any labor at all, mainly because the household
members were too old, not all households were asked to make contributions. In total 19% of
the households were not asked to make any labor contributions.10 At this time, households
were not told anything about what others were contributing, and there was no provision
point. We hired an external supervisor who monitored the construction progress and
quality, and recorded villagers' labor contributions. Thus, what we observe in this event
is the actual amount of labor contributions, and not what they promised when asked to
contribute.

<hs>  The 2011 experiment</hs>
  ~~~~~~~~~~~~~~~~~~~

While the bridge is presumably useful to all households, the usefulness varies with, e.g.,
the distance to the bridge and ownership of different vehicles. Although we have
information on the use of the bridge, it is possible that we still cannot perfectly
correct for it in our analysis. In order to avoid such potentially confounding effects, it
makes sense to also include an experiment that by design is not at all related to the
bridge. The experiment conducted in 2011 was therefore not in any way related to the
bridge or the 2009 experiment, and no reference to either the bridge or the earlier
experiment was made. While the 2009 experiment was funded by an NGO, the 2011 experiment
was conducted and funded by the University of Economics Ho Chi Minh City. There were 15
experimenters also in this experiment. They were recruited and trained in a similar manner
as for the 2009 experiment, but none of them were the same as in the 2009 experiment. The
experiment was conducted in the subjects' homes and the first part of the experimental
script read: Hello, my name is […] I'm working for University of Economics Ho Chi Minh
City, which is implementing an economic study in this village. I would like to invite you
to participate in an economic experiment, which will be conducted now. You will be taking
part in an experiment on decision-making and will earn some money by choosing among
alternatives. The experiment is designed so that your earnings will depend on your
choices, as well as on the choices of others. Your earnings will be paid to you in cash
tomorrow afternoon privately to preserve the confidentiality of your earnings. The results
from this study will only be used for academic purposes, and no other people in the
village will have information about your choices. We chose to conduct a public good game,
much like a standard linear public good game conducted in laboratory experiments. Yet, in
order to fit the setting of the village, and in order to be able to easily compare the
contribution behavior in this experiment with the other experiments, the group consisted
of all households in the village; thus, the size of the group was approximately 200
subjects. Each of these households received 200,000 dong, which was clearly a substantial
amount for them. Just as in a standard laboratory public good experiment, they had to
decide how much of the endowment to keep and how much to put into a group account. In
order to make the experiment simple to understand, each subject was told that any money
that was put into the group account would be doubled by the experimenter, and that the
total amount in the group account would be distributed to the group members, and hence to
the households. The following sentences were part of the script that the experimenters
read to the subjects. This experiment is organized with a group of 200 households
including yours. We will give 200,000 dong to each of the 200 households participating in
this experiment. Here is the agreement, which has a signature and stamp from the
University of Economics Ho Chi Minh City stating that 200,000 dong belongs to your
household. Your household and each of the other households have to decide how much of the
200,000 dong to keep and how much to put into a group account. The amount of money you put
into a group account will first be doubled by the experimenter, meaning that if you
transfer 1 dong into the group account, it will become 2 dong. The total amount will then
be divided equally between all households. The instructions included several examples, and
the subjects were allowed enough time to understand everything that was said. To inform
the subjects that their contributions would be kept completely confidential, the
experimenters told them before they made their contribution decision: “No one in the
commune, not even the officials, will know about your decision. We will keep your
contribution information completely secret.”

<hs>  Summary of the four events and household characteristics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As mentioned, the first three events were related to the bridge in the hamlet. The first
event concerned monetary contributions to build a small wooden bridge in 2005; the second
concerned monetary contributions to build a new and better concrete bridge in 2009; and
the third event concerned voluntary labor contributions to connect the road to the new
concrete bridge in 2010. The fourth event was instead a public good experiment that was
not related to the use of the bridge. The settings of the four events are summarized in
Table 1. While we designed only two experiments (the 2009 and 2011 experiments), we have
data for four different points in time, i.e., 2005, 2009, 2010, and 2011, for essentially
the same subjects. Table 2 reports background statistics, as of 2009, for the households.
There were a total of 200 households from the village that participated in the events.
However, as explained above, not all households were asked to contribute labor in the 2010
event, and in the last experiment four of the households were unable to participate.11 The
mean monthly household income is around 1.8 million dong per month. This amount
corresponds to about 95 USD per month, which is less than one USD per household member and
day. Thus, the households in the study are poor, and the average level of education is
very low. The average size of land on which a family is currently cultivating rice is also
rather small, approximately half a hectare.

<hs>  Average contributions in the four events</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Before looking at the correlations between the contributions, let us briefly look at Fig.
4, which displays the histograms of contribution in each of the events. As can be seen,
the contribution patterns are strikingly different, in particular between the 2005 and
2010 events, on the one hand, and the 2009 and 2011 events on the other. The 2009 and 2011
events have in common that they are based on windfall endowments, which may contribute to
the substantially higher contribution levels in these events.12 Comparing the 2005 and
2009 contributions, which were both in terms of monetary contributions to a new bridge,
there are thus strikingly large differences. The mean contribution in 2009 was almost
seven times as large as in 2005 (270,000 dong compared with 40,000 dong), and while almost
everyone contributed something in 2009, almost half of the households chose to free ride
in 2005. While there may be many different explanations for this, two clearly stand out:
First, as mentioned, the contributions in 2009 were based on a windfall endowment provided
by the NGO, while the contributions in 2005 were paid out of the households' existing
wealth. Second, the 2009 experiment involved a matching contribution by the involved NGO.
Such matching contributions, or seed money, have been shown to increase voluntary
contributions substantially (e.g., List and Lucking-Reiley, 2002; Karlan and List, 2007).
Moving on to the 2010 event, we can observe that even fewer chose to contribute than in
2005, in this case in terms of labor contributions. In 2010, the mean contribution of
labor was 0.5 labor days per household, which corresponds to about 40,000 dong based on an
average daily labor wage of 80,000 dong. Finally, in the 2011 experiment, there is again a
small share of people contributing nothing, where the mean contribution is substantial,
125,000 dong. The mean contribution as a fraction of the maximum contribution is actually
quite similar to the 2009 experiment; these events also share the features that they are
concerned with voluntary financial contributions to a public good and that the
contributions are based on windfall endowments. The contribution levels in the 2011
experiment are clearly unusually high compared with what is typically found in public good
lab experiments, in particular given the small marginal per capita return. There are
several potential reasons for this. Contributions in one-shot public good experiments are
typically larger than average contributions in multi-round public good experiments (e.g.,
Fischbacher and Gächter, 2010). Also, there is some evidence that non-student samples
might be more cooperative and show higher levels of reciprocation than student samples
(e.g., Gächter et al., 2004; Falk et al., 2013). Moreover, the participants in this
particular non-student sample may know each other better than most students participating
in lab experiments, and there is (not surprisingly) evidence that subjects tend to behave
more pro-socially when the social distance to the other subjects is small (e.g., Hoffman
et al., 1996). Finally, it is also possible that the fact that the experiment took place
in the subjects' homes may have induced stronger psychological pressure to contribute than
if it had been undertaken in a common venue, which appears natural given the evidence that
subjects' contributions tend to be affected by whether or not the experimenters directly
observe the contributions (List et al., 2004; Alpizar et al., 2008). Yet, we are not
primarily interested in the various contribution levels, or whether these levels are
similar across decisions. Instead we want to find out to what extents decisions are
correlated, i.e., whether or not those households that contribute more in one event also
tend to contribute more in another.

<hs>  Raw contribution correlations between the events</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As described above, we observe the contributions in each of the events at the household
level. As a first step, we therefore analyze the simple pair-wise correlations between the
four events. Remember that, for each household, we have three observations of
contributions to the bridge and one observation of contribution in a public good
experiment. We present correlation coefficients for the whole sample and for the
restricted sample of households that had the possibility to contribute in 2010. For those
that were not asked to make labor contributions, we set the contribution to zero when
calculating the correlations for the whole sample. Table 3 presents the pair-wise
correlation coefficients. Despite the large differences in contribution levels between the
events, including in the fraction that did not contribute anything, the correlation
coefficients between the four events are substantial and in most cases highly significant.
For the events related to the bridge, the largest correlation coefficients are found
between the 2005 and 2010 events. This may seem surprising since the 2005 event concerns
monetary contributions, while the 2010 event concerns labor days. Also, it seems likely
that some people have a comparative advantage in labor contributions, implying that there
is scope for a degree of specialization in contributions, which should reduce the
correlation coefficient. Our favorite explanations for the large correlation coefficient
are as follows: First, in both cases the subjects had to pay with their own resources
(money and time, respectively), and hence there were no windfall resources obtained for
the individual decision. Second, and perhaps even more importantly, both of these events
were non-anonymous, and if some people are more sensitive to the peer pressure to
contribute, then they should contribute more than others in both instances, implying a
positive effect on the correlation coefficient. Indeed, Alpizar et al. (2008) demonstrate
in a field setting that anonymity matters for charitable contributions and Andreoni and
Rao (2011) found more recently that communication per se seems to dramatically affect
altruistic behavior, primarily through increased empathy. The correlation coefficients
between the experiment in 2011 and the other three events are also substantial, with the
exception of the event involving labor contributions in 2010. Here, the coefficient is not
statistically significant at conventional levels when based on the restricted sample.
There may be several reasons for this, in addition to the fact that only one of the two is
related to the bridge: one concerns labor contributions while the other concerns monetary
contributions, one is anonymous while the other is not, and one was conducted based on
windfall money while the other was not. Yet, it is interesting to see that the correlation
coefficients between the contributions in 2005 and 2011 and between the contributions in
2009 and 2011 are large and statistically significant, despite the large differences in
set-up. Together, this clearly shows (i) that the strong correlations between the events
cannot only be due to the fact that they concern contributions to a similar good, i.e.,
the bridge, and (ii) that there is clear support for the idea that social preferences
reflect traits that to a large extent are constant over time and domains.

<hs>  Simple comparisons of Low, Intermediate and High contributors' behavior over time</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Correlation coefficients are not always straightforward to interpret, in particular as in
our case where the contribution patterns are very different between the events and where
large fractions of the subjects chose the extreme alternatives of contributing zero or the
full amount. We therefore also illustrate the stability of social preferences by
investigating how subjects who initially contributed small or large amounts in 2005
contributed in the three subsequent events. Based on the histograms above it appears
natural to classify those who contributed strictly more than 100,000 dong as High
contributors, implying that 9% of the subjects are characterized as High contributors in
2005. Since as many as 47% of the subjects contributed zero in 2005, this constitutes a
natural (albeit quite large) group of Low contributors (implying that the remaining 44%
are classified as Intermediate contributors). The subjects for the three subsequent events
were similarly classified as Low, Intermediate or High contributors. For the event in
2009, Low contributors are those contributing less than or equal to 100,000 dong (20% of
the subjects) whereas High contributors are those who contributed the maximum amount
400,000 dong (43% of the subjects). For the event in 2010, Low contributors are those who
did not provide any labor days (77% of the subjects) and High contributors are those who
provided two or more labor days (11% of the subjects). Finally, for the event in 2011, Low
contributors are defined as those who contributed less than or equal to 50,000 dong (22%
of the subjects) and High contributions are those who provided the maximum contribution
200,000 dong (40% of the subjects). Table 4 reports the shares of Low, Intermediate and
High contributors in the events 2009 to 2011 based on three different samples, those who
in 2005 are classified as Low, Intermediate, or High contributors, respectively. In
general, we find strong links between contributing behavior in the 2005 event and the
behavior in the subsequent events. Since the overall fractions of Low and High
contributors are different from each other in each of the experiments the relevant
comparisons to make are between the different samples, i.e., to compare the different
shares horizontally.13 That is, we want to compare whether those who in 2005 are
classified as a High contributors are more likely to be classified as a High contributors
in the three subsequent events than what those who are classified as a Low contributor in
2005 are. Correspondingly, we want to compare whether those who in 2005 are classified as
a Low contributor are more likely to be classified as a Low contributor in the subsequent
events than what those who are classified as a High contributor in 2005 are. As can be
seen in Table 4, the pattern follows expectation for each of the six cases. For example,
it is striking to compare the non-anonymous voluntary contributions to the bridge in 2005
with the contributions in the anonymous public good game (not related to the bridge) six
years later. Of those classified as Low contributors 2005, 32% are classified as High
contributors 2011. This can be compared with those classified as High contributors in
2005, where as many as 82% are classified as a High contributor 2011. Similarly, of those
classified as Low contributors 2005, 30% are also classified as Low contributors 2011.
This can be compared with those classified as High contributors in 2005 where as few as 6%
are classified as a Low contributor 2011. In order to formally test whether these
differences are statistically significant, we focus on the two samples of Low and High
contributors in 2005. We can then use simple Chi-square tests when comparing the
distribution of Low, Intermediate and High contributors for each of the 2009, 2010 and
2011 events. For example, we can test if there is no difference in the distribution of
Low, Intermediate and High contributors in the 2009 event for those that were Low
contributors in 2005 and those that were High contributors in 2005. In all three cases,
i.e. for each of the events in 2009, 2010 and 2011, we can reject the null hypothesis that
the distribution is independent of whether a subject was classified as a Low or High
contributor in 2005, at the 1% level.14

<hs>  Econometric analysis</hs>
  ~~~~~~~~~~~~~~~~~~~~

While the strong positive correlation coefficients, as well as contribution patterns more
generally, between contributions in the first three events (i.e., those related to the
bridge) are interesting per se, one should be hesitant to interpret these coefficients as
clear evidence of stability of social preferences. Indeed, there are several possible
interpretations of these positive correlations. For example, if the households using the
bridge the most are also willing to contribute the most (e.g., for partly selfish
reasons), we should obtain a positive correlation between contributions in the first three
events even if there are actually no differences between the households in terms of
underlying social preferences. Still, the use of the bridge can of course not explain the
correlation coefficients between contribution in the public good experiment in 2011 (which
was not related to the bridge) and contributions in any of the other events. We deal with
this problem in two ways: First, as mentioned, we run a public good experiment without any
reference to the bridge, based on the same sample. Second, we use regression techniques
correcting for possible explanatory variables that can be assumed to vary across the
households but at the same time are independent of underlying differences in social
preferences. The most obvious variable here is the use of the bridge. More specifically,
we use multivariate tobit regressions since we have non-negligible shares of subjects who
either contribute the full amount or do not contribute at all; hence, we use truncations
at both zero and the full amount for the experiments in 2009 and 2011, and at zero for the
events in 2005 and 2010. Using a multivariate model, we estimate the correlation
coefficients of the error terms for each event. These error terms are assumed to reflect
the part of social preferences that cannot be explained in terms of our explanatory
variables used in the regressions. Moreover, simple correlations do not take into account
that there were different treatments in the experiment in 2009. In order to deal with
these issues, we estimate multivariate models where the four equations are estimated
simultaneously, allowing for a correlation between the error terms of each of the
equations, and where the dependent variables are censored. We present three sets of
regressions: In the first set, we use no explanatory variables (except for an intercept).
In the second set, we use only variables reflecting the use of the bridge in the first
three events, since these variables presumably vary across the households and at the same
time are independent of underlying differences in social preferences. For the second and
fourth event we also include treatment dummy variables and experimentalist dummy
variables. Finally, we present a third set of regressions including all relevant
explanatory variables. In this last set, we thus face the risk of “over-compensation” in
the sense that there may exist variables, such as age and income, that are correlated with
true underlying social preferences. For example, suppose that all actual variations in
social preferences are determined by gender. If we then correct for gender in the
regressions, the result would indicate that there is no stability of social preferences
over time even though the actual stability through gender may be large. Yet, as is the
case when not including any explanatory variables, it constitutes a natural benchmark
case. We focus mainly on the sample of households that had the possibility to contribute
labor in 2010. However, we also report the results based on the full sample, where we have
hence set the contribution in labor to zero in 2010 for those who were not asked to
contribute. We also use the full dataset for the pairwise correlations that do not include
the 2010 event. Yet, as can be observed, the results turned out fairly similar.15 The
estimated correlation coefficients for our three sets of multivariate regressions are
presented in Table 5, for each separate event. Starting with the first three events, we
can observe that the pairwise correlation coefficients are consistently positive,
substantial, and statistically significant. Consequently, even when controlling for a
number of observable differences among households and the treatment effects, there are
strong correlations in behavior between the three events. The relative sizes of these
coefficients follow expectations in that they are generally largest when we do not correct
for any variables, and smallest when we include the full set of variables. Yet, the
differences between when we correct for the use-of-the-bridge variables and when we do not
are rather small. Again, the highest correlation coefficients are found between the 2005
and 2010 events, probably largely due to the fact that these events were not anonymous, as
discussed previously. Yet, it could still be the case that we did not manage to completely
correct for the usefulness of the bridge to different households, and that the remaining
part could explain the positive correlations. For this reason, we have the fourth
artefactual field public good experiment, which is completely unrelated to the bridge.
Here we again find a weak effect between 2010 and 2011 (we speculate about possible
reasons above), while the large and highly significant correlations between contributions
in 2005 and 2011 and between contributions in 2009 and 2011 largely prevail after
including various covariates. Consequently, we can again conclude that it is not the fact
that three of the four events concerned the same underlying good, a bridge that explains
the significant correlation between the contribution decisions. Consider next the
estimated coefficients for the covariates. Table 6 presents the results for the restricted
sample. Few of the household characteristics have a significant impact on the
contributions in any of the events and there are not any consistent patterns across the
different events (except for the use of the bridge). The contributions in 3 out of the 4
events, including the public good experiment in 2011, are positively related to the amount
of rice land owned. Monthly income, in contrast, is only positively correlated with
contribution in the public good experiment. One may speculate about the reason for the
difference. Perhaps it is more natural to relate to own income when making the
contribution decision in a non-framed public goods experiment than when making decisions
that are linked with the bridge. For the 2010 event, when people made contributions in
terms of labor time, it is not surprising that there is a negative effect of age. It is
less expected to find a negative effect of the household head being male. As suggested by
a referee, a rough, indicative story can be given as follows: One does not have to use the
bridge very much to give out of the windfall, one needs to use it a little more to give
labor (free), and one needs to use it a lot to give money if poor.

<hs>  Are the obtained correlation coefficients large?</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Yet we also find, in line with several previous studies, that contributions are highly
context dependent. Related to this, we find that some correlation coefficients are
substantially larger than others, whether corrected for other explanatory variables or
not. Perhaps most strikingly, we obtain a correlation coefficient between voluntary
monetary contribution in 2005 and voluntary labor contribution in 2010 in the order of
magnitude of 0.4 or larger, despite the fact that almost 50% contributed nothing in 2005
and over 70% (of the restricted sample that were asked) contributed nothing in 2010. Our
conjecture is that this finding may not only reflect stability of social preferences, but
also to some extent stability of what may be called sensitivity to social pressure, since
none of these events were anonymous. This is an important observation in its own right,
and calls for further research. Overall, we conclude that social preferences seem to be
quite constant over long periods of time.

<h>CONCLUSIONS</h>
-----------

In this paper we have compared voluntary contributions to a public good, in terms of a
bridge in rural Vietnam, for the same complete sample of about 200 households in a
village, at four different events spanning over a time period of 6 years. By doing so, we
have been able to avoid the potentially confounding factor related to moral licensing and
moral cleansing when measuring the extent of pro-social stability over time. Overall, we
find substantial and highly significant correlation coefficients, suggesting that pro-
social preferences are quite constant over long periods of time. Although not our main
research task, the substantial and positive correlation between the unframed economic
experiment and naturally occurring events supports the idea that social preferences
obtained in economic experiments have validity also outside the somewhat artificial
experimental context. Although our events took place in a village that is typical for this
part of the world, it is an open question whether there are large cultural differences in
the extent to which social preferences are constant over long periods of time. Previous
findings have concluded that there are non-negligible differences in the strengths of
social preferences, as measured by economic experiments, in different cultural contexts
(e.g., Henrich et al., 2005, 2010). Our conjecture is nevertheless that the extent to
which social preferences vary over time does not vary much culturally, although this is of
course an open question. For this and other reasons, we encourage further studies in the
field in order to test the robustness of our findings.


<h>REFERENCES</h>
----------

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<ART>Sufficient statistics for tariff reform when revenue matters
============================================================

Authors: James E. Anderson, J. Peter Neary
DOI: 10.1016/j.jinteco.2015.10.001
Year: 2016  |  Pages: 150-159
ASJC codes: 2002, 2003
Keywords: Generalized mean and variance of tariffs, Piecemeal policy reform, Tariff revenue, Trade policy reform

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

What kinds of tariff reform are likely to raise welfare in situations where tariff revenue is important? General conditions for welfare to rise without reducing tariff revenue are opaque. We show that they can be greatly simplified using a small number of sufficient statistics, primarily the generalized mean and variance of tariffs. We present sufficient conditions for a class of linear tariff reform rules that guarantee higher welfare without a loss in revenue. The rules consist of convex combinations of (i) trade-weighted-average-tariff-preserving cuts in dispersion; and (ii) uniform tariff cuts that preserve domestic relative prices among tariff-ridden goods.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

What kinds of tariff reform are likely to raise welfare in situations where tariff revenue
is important? The question is an important one: despite steady reductions in average
tariffs, tariff revenue is still a significant component of total tax revenue, especially
in low-income countries. Baunsgaard and Keen (2010) review the empirical evidence on the
revenue effects of trade liberalization in recent decades, and conclude that, while
middle-income countries have managed to offset reductions in trade tax revenues by
increasing their domestic tax revenues, many low-income countries have not. Even in rich
countries, the revenue effects of changes in tariffs can be substantial in absolute if not
in relative terms, and can be a factor influencing the decision to liberalize trade. The
implications of trade reform for revenue have featured prominently in discussions of the
EU's association agreements with countries in the Southern Mediterranean region (see Abed,
1998), and even in official discussions of the case for the U.S. joining NAFTA (see
Congressional Budget Office, 1993).1 Unfortunately, as we shall see, general conditions
for welfare to rise without reducing tariff revenue are opaque, and provide little
guidance to practical policy-making. Our main contribution is to show that they can be
greatly simplified using a small number of sufficient statistics, primarily the
generalized mean and variance of tariffs. Reexpressing the general conditions in terms of
these sufficient statistics leads to new operational guidelines for tariff reform that
guarantee higher welfare without a loss in revenue. The rules consist of convex
combinations of cuts in tariff dispersion that preserve the trade-weighted-average-tariff,
on the one hand, and uniform tariff cuts that preserve domestic relative prices among
tariff-ridden goods, on the other. These guidelines provide a theoretical foundation for
the standard World Bank advice to developing country clients that they should reduce
dispersion of tariffs while maintaining average tariffs to preserve revenue. In plausible
special cases, the rules require only observable data and a small number of aggregate
elasticities. Our approach builds on the sizeable literature on trade policy reform in
open economies, stemming in particular from Hatta (1977). Much of this literature provides
guidelines for welfare-improving tariff reform when government revenue is not a concern,
which amounts to assuming that the government has lump-sum tax/transfer power. This
approach has been extended to study the interplay of revenue and efficiency considerations
in trade policy reform by a number of authors, including Falvey (1994), Emran and Stiglitz
(2005), Hatta and Ogawa (2007), and Raimondos-Møller and Woodland (2015). However, these
papers either use relatively special low-dimensional models, or do not provide rules that
can be easily implementable. An exception is a branch of the literature which advocates
replacing border taxes with domestic consumption taxation. (See for example,
Hatzipanayotou et al. (1994), Keen and Ligthart (2002), and Kreickemeier and Raimondos-
Møller (2008).) The intuitive argument that the base is broader can be supplemented with
optimality considerations. Diamond and Mirrlees (1971) demonstrated that it is inefficient
to distort productive efficiency when raising revenue with distortionary taxation. Trade
taxes, by subsidizing production, drive a wedge between domestic and international
marginal rates of transformation. However, Anderson (1999) shows that gradual reform of
this type need not improve welfare when uniform radial reductions are used to lower
tariffs. The present paper admits a much broader class of trade reforms when wage taxation
is the alternative revenue source and provides more optimistic prospects for tariff
reforms which reduce dispersion. The present paper draws on Anderson and Neary (2007),
where the approach using generalized moments of the tariff structure was introduced and
applied to devising rules for trade policy reform in the conventional setting of no
revenue constraint. That paper derived linear welfare-improving reform rules as
implications of reform that reduced either or both of two sufficient statistics, the
generalized mean and generalized variance of the tariff structure. Here we extend these
methods to the case where lump-sum taxes and transfers are not feasible and so the
government faces a binding revenue constraint. All government tax changes become costly at
the margin because they involve distortions. The same sufficient statistics prove useful
in the case of an active revenue constraint, supplemented by some additional aggregate
elasticity terms. In a big step toward applicability with very limited information,
Anderson and Neary (2007) also showed that, in a special CES case, the generalized mean
and variance reduced to the readily observable trade-weighted version of these statistics.
A second contribution of the present paper is to demonstrate that observability of
generalized moments obtains with weak separability, nesting not only the CES but most
other widely-used preference and technology structures. A group of goods such as clothing
under separability can contain pairs that are complements (shirts and trousers) and other
pairs that are substitutes (cotton and silk shirts). The separable setting also permits a
further realistic extension which replaces the representative agent with heterogeneous
agents while maintaining feasible operational rules that yield Pareto improvement. Section
2 sets up the model and derives the general expressions for tariff reform in the presence
of revenue constraints. Though insightful, these do not easily lend themselves to
practical implementation. The remainder of the paper shows how they can be operationalized
using the tariff moments approach introduced in Anderson and Neary (2007). Section 3
reviews and extends that approach, while Sections 4 and 5 use it to analyze trade reform
and to derive the main results of the paper. Section 6 extends the results to the case of
many households, while Section 7 concludes.

<hs>  The setting</hs>
  ~~~~~~~~~~~

The tariff reform problem is to advise on directions of change of tariffs from initial
values. Full optimization is not feasible by assumption. The setting is a competitive
small open economy which raises its revenue with a set of tariffs and with a wage tax. For
simplicity we will present the results in terms of a perfectly competitive economy though,
as shown in Anderson and Neary (2005), the results also apply to a variety of
monopolistically competitive models with fixed entry costs and firm heterogeneity. The
wage tax is distortionary because labor supply is variable (due to household choice in an
economy where immigration is shut down) and leisure cannot be taxed. Tariffs and the wage
tax are initially set sub-optimally. The objective of the reform is to move the taxes
gradually toward their optimal (Ramsey) values. This section first describes the economy
and then derives general expressions which show how tariff changes affect welfare and
tariff revenue. These results are the key building blocks for our results in later
sections that are expressed in terms of tariff aggregates. The representative consumer's
net expenditure function is given by e(π, w, u). It gives the minimum spending needed to
sustain a level of utility or real income u when the representative consumer faces a
vector of prices of traded goods subject to tariffs, denoted by π, and a net-of-tax wage
rate denoted by w. The domestic prices π differ from world prices π* by a vector of
specific tariffs t. Since the economy is small, the world prices are exogenous, so changes
in domestic prices dπ are equal to changes in tariffs dt throughout. Implicit in the list
of arguments of e is the price of a composite export good, which we take as numeraire so
its price can be set equal to one. By Shephard's Lemma, eπ gives the vector of final
demand for traded goods, while − ew gives labor supply. As for the supply side of the
economy, the maximum value of GDP which can be produced given its technology and facing
goods prices π and a gross wage w + τ, where τ is the tax on labor income, is given by the
GDP function g(π, w + τ). By Hotelling's Lemma, the vector of supply of traded goods (or
where appropriate, minus the demand for traded inputs) is given by gπ while − gw gives
labor demand. E gives the net transfer to the private sector needed to support utility u
when domestic prices of traded goods are set at π and the wage tax is set at τ. Its
derivative with respect to π, Eπ, is the vector of excess demand for traded goods, which
equals the vector of net imports m; while its derivative with respect to τ, Eτ = − gw, is
equilibrium employment, where the maximization with respect to w ensures that the labor
market clears: ew = gw. Since e-g is concave in (π, w, τ), E is concave in (π, τ):
compensated net import demand functions are downward-sloping, and a higher wage tax
reduces employment. Here, s is the transfer from the government to the private sector. If
the government has lump-sum power, s is an active policy instrument. Otherwise, it is an
exogenous transfer, which also serves as a useful analytic link between the private-sector
and government budget constraints. Here, R0 represents the government's revenue
requirement, to fund public goods, repay foreign loans, or finance some other goal which
does not directly affect private-sector decisions. Extending the model to endogenize this
revenue requirement is straightforward, along the lines of Atkinson and Stern (1974), or,
in a trade context, Abe (1992). We do not pursue this approach here, since it distracts
from our primary focus, using summary statistics to simplify the guidelines for tariff and
tax reform. In this case, the government's revenue requirement is not an independent
constraint on policy-making because the transfer s adjusts endogenously. This makes a
crucial difference for evaluation of tariff reform: Eq. (4) leads to the standard results
of piecemeal trade policy reform, augmented to allow for an exogenous wage tax. (See
Appendix A for details.) In the setting considered in the rest of the paper, by contrast,
lump-sum transfers are infeasible, so the gradual reform problem is to determine welfare-
improving directions of change in the set of reformable tariffs t, equivalent to changes
in π, while at the same time not decreasing revenue. One class of reforms takes the wage
tax as given and looks for tariff reforms that raise both welfare and revenue. A more
ambitious class of tariff reforms permits the wage tax to vary endogenously in order to
maintain government revenue. We consider each of these classes in turn.

<hs>  The problem</hs>
  ~~~~~~~~~~~

A diagram illustrating the three-good case, two of them subject to tariffs, aids
intuition. In Fig. 1, initial tariffs are such that domestic prices equal πA,
corresponding to point A. Point F represents free trade, but of course that yields zero
revenue. Optimal revenue-raising tariffs imply Ramsey-optimal prices πR, corresponding to
point R. The tariff reform problem is to devise rules that will improve welfare locally;
directions of change for π starting from A that bring the economy closer to R in the sense
of attaining a higher iso-welfare contour.4 However, the shape of the iso-welfare contours
depends on the policy instruments available to the government. The line though point A
labeled dTa = 0 shows combinations of domestic prices that keep the trade-weighted average
tariff Ta constant. As we will see below, it is also an iso-welfare locus for the case
where the wage tax is given: i.e., it is implicitly defined by the private-sector budget
constraint (2) for given u, τ, and s. By contrast, the elliptical locus drawn through
point A shows combinations of domestic prices that keep welfare constant when the wage tax
adjusts to maintain revenue: it satisfies both the private-sector budget constraint (2)
and the government budget constraint (3) for given u (s is now irrelevant) and with τ
adjusting endogenously. This locus is one of a family of iso-welfare curves centered
around R: each raises the same amount of revenue but yields successively higher levels of
welfare as R is approached. As drawn, the locus encloses a convex set of π's and is
upward-sloping at A, but these properties are not guaranteed. To determine more precisely
the location of these iso-welfare contours and hence the desired direction of tax reform
away from A, we need to develop a more formal analysis.

<hs>  Tariff changes only</hs>
  ~~~~~~~~~~~~~~~~~~~

We will assume that this term lies in the unit interval: RI is positive and less then one.
A host of arguments has been given in the literature on piecemeal policy reform to defend
this assumption. Normality suffices, as does homotheticity or a standard stability
condition.5 Violation of the assumption would be perverse indeed, since it would imply
that a gift of foreign exchange to the private sector, enabling a rise in real income,
would at constant prices π either reduce government revenue or raise it by more than the
value of the gift. In the presence of lump-sum redistribution, moreover, a negative value
of RI would imply that gifts make the economy worse off. The left-hand side suggests a
clear presumption that more for the government means less for the private sector. However
a positive value for the term on the right-hand side can offset this presumption,
permitting a rise in both real income and revenue. This possibility arises from reforms
that remove inefficiency in the tariff structure. Below, we characterize such
possibilities in terms of tariff moments.

<hs>  The marginal cost of funds</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~

When we turn to consider choices between different forms of taxation, it is useful to
express our results in terms of the marginal cost of funds (MCF) of different instruments.
Consider the cost to the government of supporting the representative agent's real income u
with a hypothetical subsidy ds when the wage tax τ changes to raise revenue R by one
dollar. Recalling that E is concave in τ, the direct substitution effect of a wage tax on
labor supply Eττ tends to reduce Rτ below Eτ, and so encourages a value for the social
cost of funds greater than one. This could be offset by the cross effect: if leisure is a
complement for imports, so Eπτ is positive, a rise in the wage tax τ increases tariff
revenue, encouraging a value for the social cost of funds less than one. However, values
greater than one are typically found in applied studies and must be considered the norm.
Similar considerations, mutatis mutandis, apply to the magnitude of the marginal cost of
funds of any other tax instrument.

<hs>  Tariff changes compensated by wage tax changes</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Although we will hold revenue fixed, it is insightful to include the change in the revenue
requirement R0 in Eq. (12), since it allows us to interpret the coefficient of the welfare
change on the left-hand side. Consider the effect of a hypothetical transfer to the
government which reduces the revenue requirement R0 by one unit. The impact effect of this
on welfare is equal to the marginal cost of funds μτ. In an economy with tariff and wage
tax distortions this impact effect has multiplier repercussions, which are measured by the
inverse of the coefficient of Eudu. This shows that the term 1 − μτRI is the inverse of
the shadow price of foreign exchange modified for the endogeneity of the wage tax.
Moreover, as with the corresponding term in Section 2.3, we are justified in assuming that
it is positive: a negative value would imply that a gift to the economy, which relaxes the
revenue requirement R0, would lower real income.6 The intuitive implication of Eq. (13) is
that reducing tariffs on all goods for which μiπ > μτ and increasing tariffs on all goods
for which the inequality is reversed will produce a surplus. This in turn causes an
increase in real income, provided the shadow price of foreign exchange is positive. This
provides an insightful contrast with the usual expression for welfare change in the theory
of piecemeal tariff reform when lump-sum taxes are available (see Eq. (34) in Appendix A),
and it reduces to it when labor supply is fixed so a wage tax is effectively lump-sum (μτ
= 1 and Eτπ = 0). However, saying more about the tariff reform problem using Eq. (14) as
it stands is challenging. To make progress with this problem, we turn in the next section
to extend the method of tariff moments developed in Anderson and Neary (2007) to the
present context.

<hs>  Summary statistics for the structure of tariffs</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The key intermediate step in the analysis of trade reform is a decomposition of the effect
of tariff changes into their effect on various moments of the distribution of tariffs.
Anderson and Neary (2007) examine welfare-improving directions of tariff reform in the
case where revenue considerations are unimportant, so μτ = 1. Here we extend their moments
decomposition technique to the revenue tariff problem. Table 1 summarizes the notation.
Except for the trade-weighted average tariff Ta, these generalized moments and their
changes are complicated functions of consumer and producer behavior. Nonetheless, they
summarize the implications of the full matrices of aggregate demand and supply responses
in an intuitive and parsimonious way. In this respect, they are analogous to the shadow
price of foreign exchange introduced by Hatta (1977): it allows all income effects to be
summarized in terms of a single convenient aggregate statistic, whereas earlier work
typically made strong assumptions about income effects on a commodity-by-commodity basis,
such as requiring all goods to be normal.7 In the same way, the generalized tariff moments
provide a set of sufficient statistics for the substitution effects in the economy. As we
will show, analytic expressions in changes in generalized means and variances help
formulate linear tariff change rules that guarantee welfare improvement even in the
absence of detailed information about substitution effects.

<h>TARIFF CHANGES ONLY</h>
-------------------

Under separability as in Eq. (18), cuts in tariff dispersion which leave the trade-
weighted average tariff unchanged raise revenue while not harming welfare. As discussed in
Section 2.4, there is a presumption that the marginal cost of funds is greater than one
for each individual good, so it must be considered highly unlikely that this marginal cost
of funds of a composite group could be less then one. We also expect RI, the effect of a
unit gift of foreign exchange on government revenue, to lie between zero and one, as
discussed in Section 2.3. Given this, the sign of the right-hand side of Eq. (23) is
ambiguous, although there is a presumption that the direct price effect 1/μT outweighs the
income effect RI: uniform absolute reductions ordinarily imply that revenue falls: 14
Uniform absolute reductions in T raise both welfare and market access, but raise revenue
if and only if the inverse of the marginal cost of funds for all tariff-ridden goods, μT,
is less than the income responsiveness of revenue, RI. Summarizing this section, given
that very large dispersion is common in tariff structures, even in countries that raise a
substantial portion of government revenue from tariffs, Proposition 2 implies considerable
scope for efficiency improvement from dispersion cuts. On the other hand, Proposition 3
implies that absolute tariff cuts with constant dispersion decrease revenue, which creates
a presumption against average tariff reductions as part of a reform package when tariff
revenue is important (i.e., when tariffs are the only instrument).

<hs>  Tariff reform rules in terms of generalized moments</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The square bracket term is smaller than the inverse of μT under the conditions of (i), and
hence the entire expression is positive under the condition of (ii). □ Trade-weighted
mean-preserving dispersion cuts within separable goods classes; Any convex combination of
such dispersion cuts and a uniform absolute tariff change across as well as within classes
that decreases tariffs when they are over-utilized or increases them when they are under-
utilized. Proposition 5 is proved in the Appendix. The key element is that, from
Proposition 1, the condition of Proposition 4 is met under separability. The proposition
is quite useful because separability is a ubiquitous assumption in applied work. Faced
with some ten thousand tariff lines, aggregation is inevitable for any econometric or
simulation work. The proposition guarantees that trade-weighted average preserving
dispersion cuts within classes are welfare-improving without detailed knowledge of
substitution effects (either parameter values or specification) within goods classes.
National tariff schedules are full of dispersion in detailed product classes, so there is
a lot of room in practice for beneficial cuts. It is worth noting that, under
separability, a trade-weighted mean-preserving tariff dispersion cut improves welfare
strictly by raising government revenue; trade expenditure remains constant under this
reform.

<hs>  The CES special case</hs>
  ~~~~~~~~~~~~~~~~~~~~

The CES expression (31) for the marginal cost of funds reveals that the focus of
Propositions 4 and 5 on convex combinations of mean-preserving tariff cuts and dispersion-
preserving mean cuts does indeed capture all the relevant characteristics of welfare-
improving revenue tariff reform which can be guaranteed without full knowledge of
substitution effects. If exact values of η and σ are assumed to be known, it is of course
possible to improve welfare with tariff reforms outside the cones based on Eq. (31).20 As
substitution possibilities range more widely beyond the CES, more welfare-improving
revenue tariff reforms can be found which are not within the cones of Propositions 2, 3,
and 4. But again, showing that these reforms raise welfare depends on information that
this paper assumes, realistically, that the analyst is unlikely ever to have with any
certainty. Note that the CES expression sheds light on the esoteric possibility that some
tariffs may actually have a marginal cost of funds less than one. From Eq. (31), the
necessary and sufficient condition for μiπ < 1 is (1 − η/σ)Ta > Ti. The sufficient
condition requires either that η/σ < 1, substitution elasticities within the separable
group exceed substitution elasticities between that group and all other goods, or that
good i is subject to an import subsidy, so Ti < 0. Normally neither condition would be
met.

<hs>  The desirability of dispersion cuts</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Returning to Fig. 1, the ray OR through the Ramsey optimal tariff point R divides the
domestic price space into half spaces. Starting at point R, consider a mean-tariff-
preserving line (not drawn) to the uniform tariff ray OF. For points on this line between
the uniform tariff ray OF and the optimal tariff ray OR, trade-weighted mean-preserving
dispersion increases are welfare-improving. For points in the space below ray OR,
dispersion increases are welfare-decreasing. If the cone FOR is small, the World Bank
intuition about the desirability of dispersion reduction holds for most of the tariff
space.

<h>MANY HOUSEHOLDS</h>
---------------

The preceding expressions extend with appropriate modification to the case of many
households. The government budget constraint continues to hold using E for the aggregate
trade expenditure function and its derivatives, while Eh denotes the individual household
h trade expenditure function. Summing over households h, the first two terms cancel out.
The condition that reform be beneficial in the aggregate (representative agent) case is
that the third term be negative. Propositions 4 and 5 apply. The potential for individual
loss is confined to the deviation due to the balance of the first two terms. Agents can
differ in their tastes for work vs. consumption, generating differences in the aggregate
weights attached to the average tariff differentials, and they can differ in their
consumption patterns within the tariffed goods bundle when faced with the same price
vectors. The latter results in dTa,h ≠ dTa while the former results in Eπh ⋅ π ≠
(Eτh/Eτ)Eπ ⋅ π. What minimal information is needed to specify welfare-improving rules for
each household (Pareto superior rules)? Tariffs are widely levied on intermediate goods.
In this case there is no household-specific weighting, Tai = Ta, so dispersion cuts are
Pareto-superior. As for final goods, assume that imported goods in a separable goods class
have no domestic perfect substitute, and that household expenditure patterns Eπh are
observable. The former is a widely used empirical assumption because the perfect
substitutes assumption yields implications wildly at variance with the trade data. The
observability of household expenditure patterns is a more problematic assumption but it is
satisfied for a number of countries. Under these assumptions, the βh parameters can be set
equal to the household level trade-weighted average tariff Ta,h to implement the mean
preserving dispersion cut: dTh = (T − Ta,h)dα. The mechanism is a uniform deviation from
the common tariff cut rule for each household: dTh − dT = (Ta,h − Ta)ιdα. All tariffs are
changed according to dT = (T − Taι)dα. Implementation of the household specific deviations
could presumably take place at the retail level (as with food stamps or senior citizen
discounts), supplemented by some governmental identification system. Doing so, for
example, all clothing tariffs change according to the common rule, then each household
receives or pays its household specific deviation (Ta,h − Ta)dα. Alternatively, the
implementation could be done through income tax credits. To avoid shirking, the common
rule could be set around the highest Ta,h, so that all households with lower average
tariffs receive a rebate. In this scheme of tariffs, the real income of each household is
maintained, the individual variation of βh is revenue neutral since ∑h(Ta,h − Ta)π′Eπh =
0, and the government revenue will rise due to the revenue-increasing cut in dispersion.
Thus dispersion cuts are a Pareto-superior reform. As for uniform absolute cuts in
tariffs, the requirement of Propositions 2 and 3 that ‘tariffs are over (under) utilized’
becomes extremely stringent because it requires that the marginal cost of funds of the
alternative revenue source be less (more) than each individual agent's marginal cost of
funds of tariffs. This is seldom likely to appear plausible to analysts evaluating
potential reforms. The implication is that the Pareto-superiority of dispersion cuts holds
in the many household case under the separability assumption, understanding that trade-
weighted average tariffs must be calculated and applied at the household level. The
separability assumption is plausible for some goods classes and not for others. Still,
this discussion suggests the surprisingly wide desirability of dispersion cuts.

<h>CONCLUSION</h>
----------

This paper has derived rules for welfare-improving trade reform that permit confident
policy advice despite the (assumed partial) ignorance of analysts about the true structure
of the economy. Dispersion-reducing trade reform is surprisingly widely beneficial:
whenever households have implicitly separable preferences with respect to the same
partitions of goods, dispersion of tariffs within separable groups is inefficient. Cuts in
average tariffs are efficient when the marginal cost of funds of such tariffs is greater
than the marginal cost of funds from alternative revenue sources. Convex combinations of
uniform absolute cuts and mean-preserving dispersion cuts are beneficial under these
conditions. Over and above these specific results, we have shown the value of reexpressing
complex results for multi-dimensional policy reform in terms of a small number of summary
statistics. This approach should prove useful both in guiding empirical work and in
allowing an intuitive focus on the key parameters that matter for policy evaluation.


<h>REFERENCES</h>
----------

  [5] James E. Anderson, J. Peter Neary. Welfare versus market access: The implications of tariff structure for tariff reform. doi:10.1016/j.jinteco.2006.02.004
  [6] A. B. Atkinson, N. H. Stern. Pigou, taxation and public goods. doi:10.2307/2296403
  [7] Thomas Baunsgaard, Michael Keen. Tax revenue and (or?) trade liberalization. doi:10.1016/j.jpubeco.2009.11.007
  [10] M. Shahe Emran, Joseph E. Stiglitz. On selective indirect tax reform in developing countries. doi:10.1016/j.jpubeco.2004.04.007
  [12] Rod Falvey. Revenue enhancing tariff reform. doi:10.1007/BF02706015
  [14] Tatsuo Hatta. A theory of piecemeal policy recommendations. doi:10.2307/2296969
  [15] Tatsuo Hatta, Yoshitomo Ogawa. Optimal tariffs under a revenue constraint. doi:10.1111/j.1467-9396.2007.00675.x
  [16] Panos Hatzipanayotou, Michael S. Michael, Stephen M. Miller. Win-win indirect tax reform. A modest proposal. doi:10.1016/0165-1765(93)00315-F
  [17] Michael Keen, Jenny E. Ligthart. Coordinating tariff reduction and domestic tax reform. doi:10.1016/S0022-1996(01)00123-4
  [18] Udo Kreickemeier, Pascalis Raimondos-Møller. Tariff{ligature}-tax reforms and market access. doi:10.1016/j.jdeveco.2007.09.004
  [19] Pascalis Raimondos-Møller, Alan D. Woodland. Market access and welfare: Is there a conflict?. doi:10.1016/j.econlet.2014.12.012
<ART>Teacher pay and school productivity: Exploiting wage regulation
===============================================================

Authors: Jack Britton, Carol Propper
DOI: 10.1016/j.jpubeco.2015.12.004
Year: 2016  |  Pages: 75-89
ASJC codes: 2002, 2003
Keywords: School productivity, Teacher pay

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

The impact of teacher pay on school productivity is a central concern for governments worldwide, yet evidence is mixed. In this paper we exploit a feature of teacher labour markets to determine the impact of teacher wages. Teacher wages are commonly set in a manner that results in flat wages across heterogeneous labour markets. This creates an exogenous gap between the outside labour market and inside (regulated) wage for teachers. We use the centralised wage regulation of teachers in England to examine the effect of pay on school performance. We use data on over 3000 schools containing around 200,000 teachers who educate around half a million children per year. We find that teachers respond to pay. A ten percent shock to the wage gap between local labour market and teacher wages results in an average loss of around 2% in average school performance in the key exams taken at the end of compulsory schooling in England.

--------------------------------------------------------------------------------


<h>INSTITUTIONAL BACKGROUND</h>
------------------------

Education in England is compulsory between the ages of five and sixteen. While children
can be educated privately, the public (state) system dominates. State sector pupils attend
primary school from age five to eleven and secondary school from age eleven to sixteen.
Pupils can then stay on for a further 2 years to get qualifications that allow them to
undertake university level education. In 2007 approximately three million young people
(around 84% of eleven to sixteen year olds) were attending public secondary schools. In
each secondary school there are five (or seven if the school provides education up to 18)
separate age cohorts within the school at any one time. Pupils take nationally set exams
at four points during their ages of compulsory school attendance. At primary school these
are Key Stage 1 (KS1) at age 7 and Key Stage 2 (KS2) at age 11 (the year of exit), in
Mathematics, English and Science. In secondary schools these are Key Stage 3 (KS3) exams
at age 14 in Maths, English and Science and Key Stage 4 (KS4) examinations in multiple
subjects (typically between eight and twelve) at the end of compulsory schooling at age
16. We focus on KS4 (GCSE) examinations as our measure of school performance as these are
high stake examinations. For pupils they determine progress into education after age of
16, as a minimum of five pass grades required to continue on to further education, are
used by parents to choose secondary schools for their children, by the media to rank
school performance to create school ‘league tables’ and by local and central government to
identify ‘failing schools’. Schools in England are heavily regulated by central and local
government. Summary statistics on school performance have been published annually since
the early 1990's. The key measure used to compare schools has been the number of pupils
attaining at least 5 good grades in the KS4 exams (known as 5 A*-C GCSEs), though the
number of metrics published increased during the mid- and late 2000's. In addition, in-
depth assessments of the quality of the school are undertaken by the schools regulator,
OFSTED. Each school is inspected roughly every five years. Inspections often last several
days. On the basis of these site visits, OFSTED publishes a report rating the school's
performance on numerous dimensions, including an overall rating of the school and an
assessment of teaching and learning at the school. More details on these metrics are
provided below in Section 3.1.

<hs>  Teacher pay in England</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

Teacher wages are set by Local Education Authorities (LEAs) based on guidelines issued by
the national Government Department for Education.2 Despite the existence of four pay bands
(‘Inner London’, ‘Outer London’, ‘The Fringe’ and ‘The rest of England’), teacher wages
have exhibited very little regional variation relative to private sector wages since the
early 1970's. For example, the average teacher wage differential outside the South East of
England and Inner London is approximately 15%, while the equivalent private sector wage
differential can be as large than 45%.3 Since its formation in the 1990's, the School
Teacher Review Body (STRB), an advisory board which comments on teacher conditions and
pay, has frequently argued that the Department for Education should be doing more to
encourage locally flexible wages.4 Although an increasing amount of discretion over wages
has been granted to LEAs, and more latterly schools, they have not utilised the option
(Sibieta, 2015). This is possibly due to the fact that local authorities have faced strong
national teaching unions for many years, making the costs of local negotiations high for a
single school or local authority (Zabalza et al., 1979).5 Further these costs are incurred
before any gains are realised, so schools and the elected local authorities may place
greater weight on current costs versus longer-term potential gains. In addition, there has
been very little scope for schools to provide differential non-pecuniary benefits for
teachers - there is no variation in holidays and contact hours are generally fixed. Recent
changes to the schooling system in England which have come into play in the second decade
of this century have given schools potentially more power over wages and teacher
conditions. The UK government has encouraged the setting up of ‘free schools’ and
academies in England. Such schools are free of LEA control and able to choose their own
curriculum. While the programme was started under the Labour administrations which
operated upto 2010, before the school year 2008–9 there were less than 100 such schools.
The programme really accelerated after 2010 (Sibieta, 2015). To avoid contamination we
confine our analysis to before 2008 (we discuss the data in detail in Section 3.1).

<hs>  How centralised pay may affect school performance</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We follow Hall et al. (2008) and propose a simple dual-region model of the English market
for teachers. In this market, ‘The North’ has lower living costs and fewer outside options
relative to ‘The South’. Even when controlling for worker composition, the local private
sector wage is therefore lower in the North. Because of these factors, for each given
wage, teacher supply is higher in the North than in the South. An ideal pay structure
would therefore allow differential wages in each region to equalise supply and demand. As
shown in Fig. 1, by setting the centrally regulated wage to be constant across the two
regions at WC, even if on average the regulated wage is at equilibrium, a wedge exists
between it and the equilibrium wage at the regional level. In this model the regulated
wage acts as a pay ceiling in the South. This model presents the case of an invariant
regulated wage across regions. In England there is some wage variation across four large
geographical regions but, as can be seen from Fig. 1, unless the regional variation is
such that the teacher wage in the South is set equal to WS and the teacher wage in the
North is set equal to WN, the nature of the problem persists; disequilibria in local
markets will remain, affecting teacher supply in certain regions. Based on the lack of
variation that we observe in teacher wages compared with private sector wages (and indeed
the focus of the STRB on the issue), it is highly unlikely that the regional variation in
England goes far enough. This model highlights the possibility of insufficient supply in
high wage areas, but Fig. 1 would be unchanged if it were referring to the supply of
quality teachers, or indeed the supply of effort of teachers; in either case there would
remain a shortage in the South as a consequence of the invariant wage.6 This highlights
that the effect of an invariant wage on school performance in high wage areas could work
through a number of mechanisms which relate to both lower effort and the sorting of lower
quality teachers to relatively lower paid areas (Lezear, 2000). In terms of sorting,
problems may arise in recruitment and retention. First, in England, Dolton (1990) finds
that wages are an important factor in recruiting good teachers and Ma et al. (2009) find a
negative relationship between relative teacher wages and posted Local Authority level
teacher vacancies. Second, public sector wage increases in the UK have been shown to
improve the qualifications of new public sector workers (Nickell and Quintini, 2002),
suggesting the negative effect may not be seen just through vacancies, but also through
reduced teacher quality. In terms of effort, teacher quality has been shown to be
important for school performance (Barrow and Rouse, 2005; Rockoff, 2004; Benton et al.,
2003; Rivkin et al., 2005; and for England, Slater et al., 2012) and teachers have been
shown to be adversely affected by lower quality colleagues and by high turnover rates
(Ronfeldt et al., 2011). There is scope for reductions in effort in response to lower
relative wages as the nature of teaching in England means a large proportion of the work
is discretionary (time spent lesson planning, engagement in after-school programmes, time
invested worrying about particular children). Two early English studies of school
performance suggest that relative pay is important but neither test this hypothesis.
Gordon and Monastiriotis (2007) investigate neighbourhood and regional effects on
education performance and conclude that schools from some of the most affluent areas
perform worst relative to expectation. They attribute this to ‘crowding out’ of public
sector activity in affluent areas. Zabalza et al. (1979) examine English secondary schools
in the 1960s and find fewer qualified teachers and higher turnover rates in London
compared to the rest of the country and attribute this to the poor relative wages in
London.

<h>METHODOLOGY</h>
-----------

We examine the relationship between local wages and school level productivity. Our main
measure of school productivity is value added by the school in key national exams at the
end of compulsory schooling. We exploit the fact that there are national exams taken by
all students immediately prior to secondary school entry to control for initial ability of
pupils. In a set of extensions we also explore other measures of school productivity. In
our case, the inside wage is the regulated wage which is set over a large region (there
are four in the whole of England, a country with a population of around 53 million). The
outside wage is estimated from wages in the local labour market. The use of a one period
lag in wages in Eq. (1) is problematic in the context of school production in England,
where pupils normally attend the same secondary school for five years. This has two
consequences. First, since education is cumulative and final examination results will
depend on the education a pupil received in all of the years they attended the school, it
is likely that there will be long lags in the effect of the outside wage.7 Thus a
regression with only one lag in wages is likely to suffer from omitted variable bias.
While in principle we could estimate Eq. (1) with 5 lags of wages, in practise the outside
wages in year t are likely to be not dissimilar to those in year t-1, so identification of
the separate effect of each year's wages will be difficult. Second, since teachers teach
children across year groups, different year groups within one school will be subjected to
the same shocks. This is likely to create high levels of serial correlation in the outcome
data. In Appendix B we examine the impact of these two problems. These estimates show the
problem of estimating a full dynamic model, but they also confirm that in our data there
appears to be a negative relationship between outside wages and value added for almost all
lags of the wages, and that this increases over time. The explanatory variable of interest
is the gap between the school outside wage averaged over five years from t-1 to t-5 and
the regulated inside wage at time t-1. The dependent variable is school level mean KS4
points obtained at time t for school i. KS2i,t-5 is the intake performance (measured in
the last year of primary school) of the pupils who take their KS4 in year t. This boils
down to regressing changes in exam scores on changes in outside wages, keeping constant
any relevant Xit and baseline exam scores. Conditioning on the fixed effects at school
level, this is like a difference-in-difference analysis. A disadvantage is that as school
performance data which contains both KS4 and KS2 scores is only available from 2002
onwards we only have two observations per school, in 2007 and 2002, matched to wage data
starting in 1997. However, we have a large sample of schools, and the two observations per
school allow us to control for time invariant heterogeneity at school level. The outside
wages are estimated from local area data, so to deal with this we bootstrap standard
errors. Finally, as outside wages are labour market variables and not school level
variables, we cluster standard errors at the (larger) local labour market.

<h>DATA</h>
----

We use several sources of administrative data. At the core of our analysis is data on
school performance matched to data on the gap between local outside labour market wages
and the regulated inside wage. To test robustness and to examine the potential pathways by
which wage regulation may affect school output we augment this with other data on the
local labour market and teacher tenure. This section describes our data: details of
sources and the years we use are provided in Appendix A, Table A1.

<hs>  School performance data</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

Our main measure of pupil performance at school level is taken from the Pupil Level Annual
School Census (PLASC). This dataset records the performance of all pupils in national
exams in all 3285 public (state) secondary schools in England. PLASC began in 2002. We use
data from the inception of PLASC to 2007. We confine ourselves to this window to avoid any
potential contamination from schools which operated as academies (there were only 85 in
2007).8 Pupils can take up any number of KS4 exams, with a minimum of one and a
conventional maximum of around fourteen, in a range of subjects including Mathematics,
English language, English literature, Science subjects, and History.9 KS4 exams are graded
from A* to G, and these grades are translated into points, such that an A* is worth eight
points, an A is worth seven, a B is worth six, and so on. We use the total number of
points that a student obtains (i.e. points from each exam summed across all the exams they
take), averaged at school level, as our key measure of output of the school. To control
for the effect of pupil type (including effects of peers in the school), we control for
the attainment of the same cohort of pupils immediately before they entered the secondary
school.10 This is the pupils' average point score in the KS2 exams, also from PLASC. KS2
exams are graded from 2 to 5, and are taken in Mathematics, English and Science.11 In
analyses of other measures of performance we examine the proportion of pupils in the
school who achieved 5 GSCEs at grades A*-C or better; the average number of KS4 exams
taken by pupils (all from the PLASC dataset); and the number of pupils excluded from
school (from the Dept. for Education). We also use measures of school performance derived
from the in-depth inspections of schools undertaken by the government schools regulator
(OFSTED). OFSTED undertakes expert in-depth inspection of each school to provide a
published assessment of the quality of each school. These assessments take place over a
number of days and are intended to ‘net out’ any pupil or parental effect. The school's
performance is rated on numerous dimensions, including an overall rating of the school and
an assessment of teaching and learning at the school.12 Both are rated on a four-point
scale from 1 (outstanding) to 4 (inadequate). Given the frequency of inspections, these
data are available for only a sub-sample of the schools in our main analysis. We use
inspection data from 2002 to 2008. In our analysis of pathways, we use data on teacher
tenure at school level from the School Workforce Census. This is a recently released
administrative dataset from which the proportion of teachers in a school who are in post
for less than a year, and the proportion that have been in post for over 10 years can be
extracted. It has only, to date, been released for 2010.

<hs>  Wages and employment data</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~

Our key measure is the ‘wage gap’, specifically the difference between ‘outside wages’ and
‘inside wages’. Our ‘outside wage’ measure is intended to measure the alternative private
sector wage which teachers could command. We define the outside wage for each school as
the average wage of all Local Authorities (LA) whose headquarters is within a 30 km radius
of the school. This circle around the school represents a ‘travel to work’ area (TTWA), in
which teachers at the school could seek alternative employment.13 In some areas, there are
as many as 45 LAs within this radius, whilst in many others there is just one as LAs
differ in geographic size. For schools where there is not a headquarters of a LA within
the 30 km radius (or the wage data is missing for the LAs within that range) the nearest
LA with wage data is allocated to a school, provided that LA is within 60 km of the
school. If the nearest LA with wage data is outside that distance, the school is excluded
from our analysis.14 The local wage data are from the Annual Survey of Hours and Earnings
(ASHE) dataset, a 1% sample of all employees in Great Britain, covering approximately
300,000 workers per year, sampled in April of each year which provides wage data at Local
Authority level. The publicly available dataset contains average wages, split into manual
and non-manual, part and full time. As our measure of outside wages we use (the log of)
the full time male non-manual hourly earnings.15 To construct the lagged five-year average
wage for each school we use the average of outside wages from t-5 to t-1 for all LAs that
fall into the TTWA of the school. The five year gaps between our outcome observations in
Eq. (2) mean we use average wages from 1997 to 2001 and 2002–2006. In robustness checks we
use a more complex measure of outside wages which corrects wages for local labour market
composition. The correction uses Labour Force Survey (LFS) as ASHE does not contain the
necessary data to make this correction.16 Details are provided in Appendix B. Inside wages
are from the Department for Education Teacher Pay and Conditions Handbooks. For our
‘inside wages’, we use teacher wage data at the payband level to avoid concerns over
endogeneity.17 We use the (log of the) inside wage lagged for one year, so inside wages
are for 2006 and 2001. The results are robust to using contemporaneous inside wages (for
2007 and 2002). In analyses of heterogeneity we define large ‘outside wage regions’ on the
basis of the long run level of outside wages, as measured in ASHE. We group the 10
Government Office Regions (GORs) in England into three (details in Appendix Table A2,
Panel (A)) and assign each school to a single ‘outside wage region’.18 In extensions to
our main analyses, we examine the impact of outside wages and employment prospects for
different groups (the youth labour market, manual workers) in the outside labour market on
school performance. These wage and employment data are from ASHE.

<hs>  Controls</hs>
  ~~~~~~~~

The PLASC data contain information on the final-year (age 16) composition of pupils. But
our identification approach means that results with and without controls should give the
same estimates and pupil characteristics may be endogenous. So we initially present
results with no controls other than prior attainment. We then use a small set of controls
(those that we find are associated with value added controlling for outside wages) to
allow for the effect on the standard errors of heterogeneity across pupil type. The
controls we include are Key Stage 2 (KS2) scores, percentage of male students, percentage
of students eligible for free school meals (FSM), and the percentage of severe special
educational needs students (SEN) We also use this set of pupil controls to test the key
identification assumption in our design. We also include school expenditure per pupil
(EPP) to address the concern that wages might differ between schools across different
paybands, but that school resources might not.19

<hs>  Data description</hs>
  ~~~~~~~~~~~~~~~~

Summary statistics for all variables we use are in Table A3. The table shows the range of
KS4 points across school is large, with a minimum score of zero and a maximum of 99. The
mean is just under 44. KS2 scores are in different units to KS4 and have a mean of just
under 27. The log of the outside wage, averaged for each school over a five-year period,
has a school level mean of 7.134, which equates to an average salary of £29,524 per
annum.20 The log of the inside wage has a mean of 6.43 and on average the wage gap is
0.704. All variables, particularly the wage gap, exhibit considerable within group
variation, indicating change over time within schools. Table A2, Panel (B) shows the
absolute growth in the (nominal) level of wages by the three outside wage regions for the
whole period covered by our data, 1997–2006. For the whole period, absolute growth is
highest in the high outside region at £12.2 K and lowest in the low wage region at £8.4 K.
In the first sub-period, the growth is again monotonic across the three outside wage
regions. In the second sub-period, the growth is highest again in the high outside wage
region and very similar in the medium and low wage regions. Given this, there is a close
mapping between the definition of broad outside wage region in terms of long run levels of
wages and a definition of outside wage areas in terms of growth rates in wages.21 Table 1
presents cross sectional estimates year by year between the (log of) the wage gap (lagged
one year) and school average GCSE performance. We include controls for mean KS2 scores at
intake and local authority fixed effects. The estimates are the change in average GCSE
points per pupil associated with a 10% increase in the outside wage. All the cross-
sectional associations are negative, though not all are statistically significant. The
association is largest in 2005 at just over half a GCSE point lost per student.

<hs>  Test of assumption that school fixed effects can be differenced out2222We are grateful to an anonymous referee for making this issue clear and for suggesting tests to address this. This section draws heavily on their help.</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The model we estimate is a model of value added i.e. we condition on the prior attainment
of the pupils who are in the school at age 16. We assume that the school fixed effects in
Eq. (2) are fixed over time and so can be differenced out. This assumption may be violated
for several reasons. The most important of these is that the cohort of students whose KS4
achievement is measured in 2007 is different from the cohort whose KS4 achievement is
measured in 2002. This is particularly a problem in our context if within school
differences in cohorts are correlated with changes in wages and different types of student
different in expected growth in achievement. We seek to overcome this, in part at least,
by defining the outside wage as covering a large area compared to a school. The travel to
work area in our analysis is 30 km round the school. Thus the wage we use is not the wage
simply of workers who live locally to the school. This means that the outside wage is less
likely to be a measure of the wage of parents of the children in the school. We also
control for a number of observed characteristics of the children in the each of the two
cohorts. However, we may be concerned that our design is not robust and here we implement
a direct test of our assumption that changes in the outside are not correlated with
observable changes in the school cohorts. We regress, at school level, the initial level
of the achievement of the school cohort KS2i,t-5 plus the other covariates pertaining to
the school cohort, on the outside wage, controlling for school fixed effects and time
dummies.23 We present results for all years 2002–2007 and also for 2002 and 2007 only. In
our main estimates of Eq. (2), we use two observations per school of value added. The
dates of these are 2007 and 2002 and therefore the school level covariates we use in our
regression are 2006 and 2001. The results are in Table A4. The table presents the
estimates of KS2i,t-5 and the other student characteristics we use in the main results on
the outside wage along with the joint F-test of all the covariates. Column (1) presents
results for the whole period and column (2) for 2002 and 2007. The results show that the
F-tests on the covariates in both columns are small and insignificant. In addition, none
of the student characteristics are significant associated with the outside wage across the
two regressions. It is possible that areas with high wage changes experience differential
changes in school composition over the period than areas that had lower wage changes. To
examine this we repeat the analysis above, but this time splitting the sample split into
three groups according to the growth in outside wages over the period.24 This split into
three regions according to wage growth rates has very close correspondence to a split in
terms of long run levels of wages. The results are presented in columns 3–8 of Table A4.
This shows that there is a little more association within ‘growth in outside wages’
regions between the pupil characteristics and the level of wages, but even here only two
of the F-tests are statistically significant at the 5% level. Further, the patterns of
association between changes in pupil characteristics and changes in wages is not
consistent across, or within, regions. For the highest ‘growth in outside wages’ region,
wage growth is associated with an increase in the proportion of children with parental low
incomes, as measured by eligibility for free school meals. In the lowest ‘growth in
outside wage’ region, an increase in wages is associated with a fall of pupils with
special needs, which might also be taken as a marker of low parental income. But in this
region a growth in wages is also associated with a fall in performance in the exams taken
immediately prior to school entry (Key Stage 2).25

<hs>  Tests of common trends</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

Our analysis is essentially a difference-in-difference (DiD) estimation in which we have
multiple areas and two years per school. To check our common trends assumptions we regress
the growth in outside wages between 2002 and 2006 at the LEA level on the average
characteristics of school pupils (jointly) in 2002 and the level of total KS4 points per
pupil in 2002 (the earliest year for which these data are available). Differences in
outside wage growth that are associated with the initial level of covariates or school
output could indicate that areas that differ in terms of wage growth also differ in terms
of unobservables and threaten our identification strategy. The results are presented in
Appendix A, Table A5 columns [1] and [2]. The results show that there are no significant
associations between the 2002 characteristics and the subsequent wage growth at LEA level.
While the baseline school covariates and school level average GSCE points are not
available before the release of PLASC in 2002, there is available data on the performance
at school level on the 5 A*-C metric. As a further test, we examine the association
between this metric in 1997 with subsequent wage growth 1997–2006. This therefore spans
the full period covered by our wage data (as our analysis uses wages averaged over 5
years, lagged once). The results are presented in Appendix A, Table A4, column [3] and
show no association between baseline performance and wage growth. The subsequent columns
of Table A4 repeat these analyses at the level of the three outside wage regions. Again,
we find no association between baseline covariates or baseline school performance and
subsequent wage growth. We conclude that our design assumptions are likely to be
satisfied.

<hs>  Baseline results</hs>
  ~~~~~~~~~~~~~~~~

Table 2 presents estimates of the effect of wages on school productivity as measured by
value added on KS4 test scores. Standard errors are robust, clustered at the TTWA level
and bootstrapped to allow for the estimation of outside wages.26 Columns [1] – [4]
presents the results for value-added (total exam points per pupil controlling for initial
intake scores). Columns [5] and [6] present results for the percentage of pupils who
achieved at least 5 A*-C GCSEs (also with controls for initial intake scores). Columns [1]
and [2] present OLS estimates. The remaining columns present fixed effects estimates. The
first of each pair of estimates has no controls and the second includes those pupils and
school level covariates which are associated with test scores after controlling for school
fixed effects and prior attainment. The table shows all coefficients on the wage gap are
negative and significant. The increase in size between the OLS and fixed effects estimates
in Columns [1] and [2] indicates that controlling for omitted school level factors is
important.27 On the other hand, the effect of controlling for time varying school level
covariates is small, supporting the appropriateness of our identification strategy, as if
this is correct the covariates should only affect the standard errors. The coefficients
represent the estimated change in the outcome associated with a 10% increase in the gap
between the five-year outside average wage and the inside wage. Column [4] indicates a
loss of approximately 1 GCSE point per pupil in value added in response to a 10% increase
in the wage gap, which is equivalent to dropping one GCSE grade in one subject or around a
2% average fall at the mean of 44 points. Column [6] indicates a fall of around 2.5%age
points in the proportion of pupils achieving 5 or more A*- Cs, which equates to a 5% fall
at the mean of 56.5 percent. Thus the estimates suggest that a positive shock to outside
wages leads to a small, but non-trivial, fall in both measures of school productivity. We
now subject our results to a battery of tests. We begin by testing the robustness of the
results to the definition of our key variable, the outside wage. We then allow for
correlation of errors across schools within labour market areas. We then test the salience
of our design by examining whether the effects of regulation are larger in various
settings in which the wage ceiling should have greater bite. Finally we examine robustness
of the results to potential gaming by schools that may be correlated with the outside
labour market shocks.

<hs>  Alternative specification of the outside labour market</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our primary specification uses the average of the one year lagged gap between the (five
year averaged) non-manual male outside wage for a TTWA defined as 30 km round the school
and the regulated (inside) wage. We subject these key measures to a number of robustness
tests. First, in the spirit of a placebo test, we check that there is less response to a
less relevant measure of outside wage. As teachers are graduates, if the outside wage has
an effect on their performance, they should be less likely to respond to shocks to the
wages of less skilled workers. In row [2] of Table 3 we replace the non-manual wage with
the wages of less skilled workers (manual workers). We find the coefficient on the wage
gap more or less halves and is insignificant at conventional levels. Second, we check
robustness to the definition of the TTWA. Our main specification uses a radius of 30 km
round each school to define each school's unique TTWA. We change this radius in 10 km
steps from a minimum of 10 km to a maximum of 120 km. The estimated wage coefficient for
each radius and the associated 95% confidence intervals are plotted in Fig. 2. This figure
clearly shows the results are insensitive to the precise choices of the radius for
distances between 20 and 60 km. Larger areas cannot really be considered to be a TTWA for
a school and we also find no effect at the very small radius of 10 km. It is possible at
this small radius wages are endogenous; we return to this below in Section 5.3.28 Third,
outside employment prospects may matter as well as wages. At the very least, if employment
falls, average wages rise due to composition effects. To check whether this impacts on our
results we add the employment rates of 25–49 year old at the local authority level over
the 5-year period for which the cohort is in school as an additional control. Row [3]
shows that the coefficient on the wage gap falls a little but remains significant at the
10% level. The coefficient on the employment rate is insignificant. Fourth, our model is
driven by the difference between inside and outside wages. The inside wage at school level
may be endogenous if schools try to circumvent wage setting. To test this we omit the
regulated wage and estimate the effect of only the outside wage. The results in row [4]
indicate that the coefficient on the outside wage is actually very little different from
that on the wage gap in our baseline estimates in row [1], though inclusion of the
regulated wage improves the precision of our estimates. This suggests that the average
school was not able to the circumvent wage regulation.29 Fifth, we use a more
sophisticated measure of outside wages that creates an area- and time-specific outside
wage for teachers using the observed characteristics (age, gender, years of schooling,
etc.) of teachers in a particular area-year cell (we do not observe these characteristics
at the school level).30 The results in Row [5] show that this has little effect on the
estimated wage coefficient. Examination of the adjusted wage series shows that the
difference in characteristics between teachers and those working in other sectors does not
vary greatly over time in an area (available from authors). Thus the main cause of area-
specific time-series changes in the wage gap is simply the growth in the non-manual wage
in an area rather than changes in observables or the price of these observables over time.
This supports our use of a measure that does not adjust for composition. Sixth, there may
be common unobserved shocks to wages at the local geographical level (the TTWA). To allow
for this, we use spatially correlated standard errors as in Conley (1999). Row [6] shows
the estimates remain significant at the 5% level. Finally, wage changes in an area may
lead to school composition changes, both at intake at age 11 and during the 5 years in the
run-up to Key stage 4 exams if children change school between the ages of 11 and 16. We go
some way to picking this up by controlling for KS2 and other characteristics of the school
cohort who sit the KS4 exams. But there may remain unobservable time-varying changes in
the school cohort which we cannot control for with school fixed effects (as they are not
time varying) or may not control for with the cohort level time-varying measures of
initial ability (KS2 mean) and other pupil characteristics. Estimates without controls for
KS2 provide some indication of whether unobservable changes in ability might affect our
results. In Row [7] of Table 3 we present results without controls for KS2. These are
about 20% higher than our baseline estimate. This suggests that if an increase in wages is
negatively correlated with changes in unobserved post-intake ability of the school
population, our estimated effect may be a biased upwards. On the other hand, if changes in
post-intake unobserved ability are positively correlated with shocks to wages, then our
estimates will be biased towards zero. Arguments can be made for both a positive
correlation (parents can buy more goods to complement schooling) and a negative one
(parents who have an income shock substitute towards paid work and have less time to
supervise their children).

<hs>  Tests of the salience of our research design</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our argument is that pay regulation acts as a ceiling and we exploit this to identify the
impact of pay on school productivity. However, we do not observe what the unregulated wage
for teachers would be. While it is difficult to estimate the exact counterfactual wage for
a teacher in the outside labour market (see Ma et al., 2009, for one approach) even
without observing this counterfactual we should expect to find more effect where the
ceiling is more likely to bite. This is in labour markets where outside wages are highest
and where schools have least power over wage setting and conditions of employment. To
compare the effect of an outside wage shock across heterogeneous outside labour markets we
estimate the response to an outside wage shock separately for schools in each of the three
‘outside wage regions’. The results presented in Table 4 show a monotonic relationship
between the wage gap and reduction in value added. Column [1] of Table 4 shows a negative
interaction term for the highest wage region. Column [2] shows a positive interaction term
for the lowest wage region. Column [3] presents estimates for each outside wage region
separately. These confirm the results of the previous two columns: the effect of pay is to
reduce school productivity most where the pay regulation bites hardest and to not affect
it where the wage gap is small.31 These results fit with the pattern in regional wage
changes that were discussed in Section 3.4. While London and the South East may have the
highest long run level of outside wages, our estimates recover a response to shocks to
outside wages. These have been largest in the high ‘outside wage’ region but they also
have arisen in several labour markets located in the middle ‘outside wage’ region. For
example, of the LAs in the top quartile of highest wage growth in our period, 35% are in
the middle ‘outside wage’ region. For these LAs our estimates of the counterfactual wage
(what would be paid in the absence of regulation) is £1750 higher than the regulated
wage.32 Thus wage regulation bites in the middle, as well as the highest wage area, and we
find a response to wages in both.33 We also check that our results are not driven by
London schools. Column [4] of Table 4 omits all London schools and shows are results are
not ‘a London effect’. The point estimate of a wage shock for such schools is around 30%
higher, though the difference with the full sample is not statistically significant. We
would expect a larger effect for schools which have least power over their terms and
conditions of employment. Other schools might try to circumvent the regulation in a way
that would lead to a smaller impact of the wage gap for such schools. In England,
secondary schools are classified into a number of types, the most common being Community
Schools. These schools are not permitted to select pupils and LEAs have control over their
curriculum and teacher wages. In the other types of state schools pupil selection is
sometimes an option (for example, publicly run religious schools) and there is, in theory
at least, more flexibility in terms of teacher wage setting. In columns [5] and [6] we
present the estimates for Community Schools only. Column [5] is for KS4 results and column
[6] for the 5A*-C proportion. The magnitude of the coefficient increases in each case by
around 30% compared to the estimates for all schools. These results provide support for
our argument: there is a stronger effect amongst schools with the least (no) power over
their wage setting which is where the gap will bite hardest.34

<hs>  School gaming</hs>
  ~~~~~~~~~~~~~

KS4 exams are high stake exams, not just for children, but also for schools. This may lead
to school gaming and if this is associated with higher wage growth it could bias our
results. By looking at both a measure of average performance (adjusted for intake) and
performance on the key 5 A*-C metric, which matters most for lower ability students, we
look at performance at different parts of the ability distribution. So if gaming only
affects the performance of low or high ability students, our approach should deal with
this. But to further investigate this we first consider whether schools subject to wage
shocks try to prevent children from sitting exams by excluding them. We can examine this
only at regional (the 10 GORs) level due to lack of published data on exclusions at the
school or LEA level.35 The results of a regression of wage shocks on exclusions at the
regional level are presented in Table 3, row [8]. This shows no relationship between the
outside wage and the number of exclusions, suggesting schools do not react to wage shocks
by baring pupils from exams. Second, it is possible that schools react to outside wage
pressure by limiting the number of exams that pupils take in order to get better average
performance. To examine this we re-estimate our baseline model using the average number of
exams taken as the dependent variable. The results in row [9] show that schools do respond
at this margin: a 10% increase in the outside wage causes schools to reduce the average
number of exams taken by each pupil by just over 0.16. They may be doing this to hit the
key 5 A*-C metric. However, as Table 2 shows, this strategy does not appear to prevent
them from having lower performance on this metric. But it may mean that our results are
under-estimates of the impact of the outside wage: schools subject to shocks may divert
more of their effort to hitting the targets at the expenses of higher scores above the
target.36 We conclude that while wage shocks may induce schools to game, gaming does not
drive our results. Schools subject to wage shocks do not exclude pupils to avoid poor
performance and while they reduce the number of exams their pupils take, wage shocks still
negatively affect performance at both the high end (students who take many exams) and at
the lower end (those students aiming for the 5 A*-C minimum) of the ability distribution.
On the basis of this battery of tests, we conclude that our identification strategy is
robust. School performance is decreased by positive shocks to wages in the local labour
market, there is an effect for both high and low ability pupils, and the effect is
stronger where the wage ceiling has more bite.

<h>MECHANISMS</h>
----------

Our argument is that shocks to outside wages can drive teacher effort (through an
efficiency wage effort) and labour supply (the loss of good teachers) and that this lowers
the quality of teaching. But it is possible that the results are not due to responses of
teachers but are driven by responses of pupils and their parents to outside market
conditions. While we cannot rule this out completely, we provide descriptive (as it is
mainly cross-sectional) evidence on this by examining a measure of teacher quality that
should not be affected by pupil type, so shutting down a pupil effect; we directly examine
the relationship between wages and teacher tenure to see if schools subject to wage shocks
experience problems with teacher retention; and we examine whether the plausible responses
of pupils to outside labour market conditions drive our results. Finally, we discuss
evidence relevant to parental behaviour.

<hs>  The effect of wage regulation on quality of teaching</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

One way to examine the effect between wages and quality of teaching would be to examine
the qualifications of teachers. However, teacher qualifications are not likely to be a
useful margin. First, research on teacher qualifications suggests there is little
correlation between teacher qualifications and teacher effectiveness (e.g. Rockoff, 2004,
Rivkin et al., 2005, Aaronson et al., 2007, for the USA and Slater et al., 2012, for
England). Second, in the LFS data, most teachers are graduates and this figure does not
vary systematically across regions. Instead we examine a direct measure of the
effectiveness of teaching in the school: the ratings the school received in their OFSTED
inspection of school quality between 2003 and 2008. This measure should be less
contaminated by unobservable (to us) attributes of the student body as the regulator
ratings are based on in-depth inspections of the school carried out by experienced
educators. School performance is rated on a number of dimensions, each using a four-point
scale which ranges from 1 (outstanding) to 4 (inadequate).37 In Table 5, column [1] we
examine the relationship between overall performance of the school and outside wages and
in column [2] we examine the relationship between the ‘quality of teaching’ score and
outside wages.38 We use the same lagged five-year average definition of outside wages and
include pupil characteristics for the year of observation as in our baseline model. As
there is only one observation per school we do not include school fixed effects but
instead include LEA fixed effects. The results show that a larger wage gap is associated
with a poorer overall rating of the school (a positive coefficient indicates an increase
in wages is associated with poorer performance). More importantly, it is also associated
with poorer teaching quality. A 10% increase in the local labour market wage decreases the
quality of teaching by 1.4 points.39 This is a large effect: the mean teaching quality
score is 2.6 so this is a fall in the teaching quality score of over 50% at the mean.

<hs>  The effect of outside wages on teacher tenure</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In our model, one effect of wage regulation is that teachers leave schools in high wage
areas. This is likely to affect student performance through a variety of routes: time will
need to be spent by the senior management team on recruitment rather than other
activities, less experienced teachers may be less effective (Dolton and Newson, 2003,
provide UK evidence on this) and there may be spillovers on the morale of the remaining
teachers that may dampen effort (Ronfeldt et al., 2011). To look at this channel (which is
essentially selection) we examine the relationship between outside wages and teacher
tenure in each school.40 We exploit a recently released data set, which presently covers
only 2010. We cannot, using these data, examine hires and separations, but we can examine
the association between average tenure in schools in time bands and outside wages. We
present the association between the proportion of the teachers who have very short tenure
(less than a year in the school) and long tenure (over 10 years in the school) and lagged
outside wages, averaged over five years to replicate the modelling of wages in our
baseline specification.41 We only have one observation per school so estimate Eq. (2)
using LEA rather than school fixed effects, and report the results in Table 5, columns [3]
and [4]. Column [3] presents estimates of wages on short tenure while column [4] examines
long tenure. The results show that where outside wages are high, schools have a higher
proportion of teachers who have been in tenure less than one year and a lower proportion
of teachers who have been in tenure for ten years only. The wage effect is little altered
by controls for pupil type.42 A £1000 increase in the outside wage results in a 0.25
percentage point increase in the proportion of teachers who have been in the school less
than a year, and a 0.43 percentage point decrease in the proportion of teachers who have
been in the school more than 10 years. While the magnitude of these effects is not large
(the coefficients represent a 2% change for both short and long tenure), schools in high
wage areas lose teachers faster and also have less experienced teachers.

<hs>  A pupil or parental effect?</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~

An alternative hypothesis is that our results are due to the responses of pupils and/or
their parents to outside wages. The relationship we find could be driven by pupils
responding to better labour market opportunities by decreasing their effort at school
because they know there is an employment alternative. If this is the case, we would expect
to find a negative relationship between school performance and higher outside wages and/or
the demand for youth labour in the local labour market. To examine this we estimate the
relationship between school performance and the demand for youth labour, as measured by
local authority wages and, separately, the unemployment rate, of 16–25 year olds, lagged
one year.43 Regressions are at school level and include the same controls as our baseline
specification and school fixed effects. Table 5, column [5], presents the results for the
association of school performance and youth wage rates. Column [6] presents the
association with youth unemployment. Neither association is large or statistically
significant. Further, for the negative relationship we find between outside wages and
school performance to be driven by a pupil response, pupils would have to be responding
negatively to positive outside wage or employment shocks. Whilst this is plausible, it
seems equally plausible that at least some pupils respond to positive wage shocks by
putting in more effort at school, on the grounds that if they get better exam grades they
are more likely to get a (better) job. These plausibly heterogeneous responses do not fit
with our finding of a negative outside wage effect for both low ability students (those at
the 5 A*-C margin) and all students (total exam points achieved). An outside wage shock
would also be a positive shock to parental income, which could result in worse performance
if greater parental income means less supervision of children or more leisure time for
children. While we cannot rule this out, the lack of significance of the full time male
manual wages in the robustness checks in Section 4 brings into doubt whether the effect is
working through parental income. If parental income was important, it is not clear why a
parental income effect should operate only for parents in non-manual occupations. In
addition, the large (though often correlational) literature shows a positive rather than a
negative association between parental income and child attainment. It thus seems less
likely that the negative relationship we find between outside wages and child attainment
is driven by a parental effect. School performance could affect outside wages, which would
bias our results. The most obvious mechanism by which school performance may affect
outside wages is through sorting: good schools attract high income parents to move into
the area surrounding a school.44 This would give a positive shock to the average outside
wage and would bias our estimated coefficients upwards. However, the 30 km radius TTWA we
use weakens this argument. If we had used the catchment area of a school to determine the
outside wage this would be problematic, as parents try to buy houses in the catchment
areas of ‘good’ schools. But much of that gaming is within area. Individuals are likely to
choose areas based on their job and general lifestyle choice and then select their
specific within-area locations based on the schools available. Fig. 2 shows a smaller
relationship between outside wages and school performance at radii of 10 km and at 20 km.
The TTWA radii at these distances give more weight to the local catchment area round each
school, which may indicate endogeneity at this smaller spatial distance. Our analysis uses
30 km distance to avoid this problem.45 In summary, whilst these results are primarily
descriptive as data limitations mean they rely on more restrictive assumptions than our
main analyses, they suggest that the effect of shocks in outside wage on school
performance is, at least in part, through lower teaching quality and labour supply and not
from responses of parents and children to the local labour market. In fact, whilst pupils
(and their parents) might respond, they probably do so in a way which biases our estimated
coefficients towards zero.

<h>CONCLUSIONS</h>
-----------

This paper exploits the national regulation of teacher wages, national exams at entry into
and exit from secondary (middle/high) schooling and a national school inspection system in
England to estimate the effect of teacher pay on school productivity. We find that a
larger gap between regulated pay and the outside labour market remuneration reduces school
performance as measured by student performance in key exams and that the effect is larger
where the ceiling imposed by regulation bites harder and for schools that have no control
over pay and conditions at school level. At the average a 10% increase in the local labour
market wage would result in an average increase of 2% in the scores attained in the high
stake exams taken by pupils at the end of compulsory schooling in England. But the effect
in areas or schools where the ceiling bites harder is around 30% higher.46 Lazear (2000)
emphasises that incentives can affect performance through both effort and sorting. The
national set up of the wage regulation in England means that both channels are likely to
operate. Wage regulation which keeps teacher relative wages low in one (large) area of the
country and high in other (large) areas will encourage both effort reduction and mobility
of teachers to area where they get better relative remuneration for the same job. Data
constraints mean that we cannot trace through all the pathways through which the pay
effect operates but it seems likely that both channels operate. We have shown that school
performance and direct measures of the quality, which are important to schools under the
‘name and shame’ rating system used at national level in England, are lower in schools
where regulation bites harder. This may reflect reduced effort of the teachers in the
schools but we also show that schools subject to high outside wages relative to regulated
pay also have higher staff turnover, which may reflect movement of teachers away from
these areas. Our findings support the view that teacher pay is important for school
performance. The recent focus of many governments has been on using pay for performance
for teachers (e.g. Lavy, 2009). However, centralised pay setting affects teachers in many
more countries than are using pay for performance in the classroom. Our findings suggest
that policy effort could be usefully directed towards increasing flexibility in these
centralised wage setting processes.


<h>REFERENCES</h>
----------

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<ART>The Elephant In The Ground: Managing Oil And Sovereign Wealth
=============================================================

Authors: Ton van den Bremer, Frederick van der Ploeg, Samuel Wills
DOI: 10.1016/j.euroecorev.2015.10.005
Year: 2016  |  Pages: 113-131
ASJC codes: 2002, 2003
Keywords: Hedging, Leverage, Oil extraction, Prudence, Sovereign wealth fund

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

One of the most important developments in international finance and resource economics in the past twenty years is the rapid and widespread emergence of the $6 trillion sovereign wealth fund industry. Oil exporters typically ignore below-ground assets when allocating these funds, and ignore above-ground assets when extracting oil. We present a unified stylized framework for considering both. Subsoil oil should alter a fund's portfolio through additional leverage and hedging. First-best spending should be a share of total wealth, and any unhedgeable volatility must be managed by precautionary savings. If oil prices are pro-cyclical, oil should be extracted faster than the Hotelling rule to generate a risk premium on oil wealth. Finally, we discuss how our analysis could improve the management of Norway's fund in practice.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Since 1994 the number of sovereign wealth funds has nearly quadrupled to 73 (SWF
institute, 2013). These funds hold some of the largest portfolios in the world and
globally account for over $6 trillion in assets (ibid.). Two thirds of the sovereign
wealth fund industry (by size) has been funded by selling below-ground assets such as oil,
natural gas, copper and diamonds (“oil” for short). These funds often comprise a large
part of commodity exporters’ wealth. Azerbaijan’s US$ 34 billion fund accounts for almost
half its GDP, Qatar’s US$ 170 billion fund accounts for almost two thirds of GDP, Saudi
Arabia’s US$ 740 billion funds are approximately four-fifths of GDP, Norway’s US$ 840
billion fund is nearly one and a half times GDP, and the United Arab Emirates’ US$ 1
trillion funds are over two and a half times its GDP (SWF Institute, 2013; IMF, 2013). The
purpose of these funds is to smooth consumption of oil income: across generations because
oil reserves are finite, and between periods because oil and asset prices are volatile.
While such funds are professionally managed and often allocate their assets using modern
portfolio theory, we argue that their investment strategies do not take due account of oil
price volatility and subsoil reserves. Similarly, existing theories of optimal oil
extraction do not take into account volatile financial markets. These are important issues
for resource exporters, since commodity prices are notoriously volatile and below-ground
assets can be worth much more than the above-ground fund. Our aim is therefore to answer
four questions about how below-ground resources should influence above-ground portfolios,
and vice-versa. Firstly, how should one allocate above-ground assets given a volatile
stock of below-ground assets? Secondly, how quickly should financial and oil wealth be
consumed? Thirdly, how does this change if financial markets are incomplete, so that oil
shocks cannot be completely hedged in the portfolio? Finally, how should the optimal
extraction rate of below-ground assets be affected by risky above-ground assets? We will
show that policy-makers should adjust their above-ground portfolios to accommodate the
volatility and erosion of below-ground oil stocks (hedging and leverage effects
respectively); consume a fixed share of total wealth; manage shocks that cannot be hedged
with precautionary savings; and, if the marginal rent from extracting an additional barrel
of oil, namely the oil price minus marginal extraction costs, co-varies positively with
average equity market returns, then oil should be extracted faster. Our analysis combines
three large and previously unrelated strands of literature. Firstly, the allocation of
financial assets is described by CAPM equations modified for subsoil oil wealth. This
extends the continuous-time analysis of optimal consumption-saving and portfolio choice
(Merton, 1990).1 Secondly, consumption is described by a stochastic Euler equation,2
extending the literature on prudence and precautionary savings to the case when both
financial assets and oil extraction can be chosen.3 Thirdly, the optimal rate of oil
extraction is described by a stochastic Hotelling rule modified if the proceeds of
extraction of below-ground wealth are invested in a risky above-ground financial
portfolio.4 Our intended contribution is to introduce a stylized framework that combines
canonical insights from all three of these fields. These insights would be modified by
including transaction costs and illiquidity premiums, which would help to explain why in
practice fund managers do not adjust their portfolios too frequently by introducing some
mean reversion into the portfolio decisions (Constantinides, 1986; Acharya and Pedersen,
2005; Garleanu and Pedersen, 2013; Jong and Driessen, 2015). This paper is laid out as
follows. Section 2 introduces our model for portfolio choice, saving and oil revenues.
Section 3 shows how to allow for below-ground oil wealth with a predetermined path for oil
production when the oil price is completely spanned by returns in asset markets. Section 4
deals with the case of investment restrictions which prevent the oil price being fully
spanned. Section 5 derives the optimal path for oil extraction. Section 6 discusses the
implications of our results and compares these with the policies adopted by the Norwegian
fund. Finally, Section 7 concludes and qualifies our results.

<hs>  Additional precautionary saving</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The wealth effect describes the change in the expected return on total wealth from not
investing in a particular asset (see (15)). If an asset cannot be held by the fund (cf.
asset h in (15)), there is still some exposure to it embodied in the oil price. With
complete markets this exposure is offset inside the fund, so the net exposure is a
constant share of total wealth. With incomplete markets this net exposure cannot be fully
offset and will earn a rate of return, changing the expected return on total wealth. Its
importance will diminish as oil reserves are depleted.

<hs>  Stylized illustration of oil-CAPM model</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We now illustrate how a sovereign wealth fund is affected by the presence of subsoil oil,
depending on whether or not it has access to hedging assets. We suppose that there is a
risk-free asset, r, and two risky assets: 1 uncorrelated with the oil price (the market
asset) and 2 perfectly negatively correlated with the oil price (the hedging asset).23 To
ensure the latter asset is used for hedging only, we assume it has a zero excess return.
This focuses our attention on the precautionary effect (and sets the wealth effect to
zero). Fig. 1 first gives the declining expected paths of oil revenues and oil wealth and
their 95% confidence bounds. Fig. 3 indicates that the consumption path is smoothed in
face of declining and volatile oil revenues and grows in line with total above- and below-
ground wealth to reflect precautionary saving. As oil wealth is run down (red dotted line
in panel (b)), the fund is built up (blue dotted line) reflecting the basic insight that
total wealth should grow at the same constant rate, if the oil price is completely
spanned. Investment restrictions: incomplete markets Now consider the situation where the
fund is prevented from investing in the risky hedging asset 2 or, equivalently, going
short in an asset that correlates positively with the oil price. The dashed lines in Fig.
2 describe the case with investment restrictions, and indicate that the portfolio weight
of the uncorrelated asset 1 is unaffected by restrictions on investing in the hedging
asset (see (8)). The difference arises merely from the change in the drift of the fund F
due to the precautionary effect discussed below. By restricting investment in the hedging
asset (or, equivalently, preventing short positions in an asset that is positively
correlated with the oil price), there is less need to borrow the safe asset (assuming pure
hedging assets with zero excess return as in the numerical illustration, thus avoiding
wealth effects). Residual volatility will then be managed by additional precautionary
savings. The effect of incomplete markets on consumption is illustrated by Fig. 4 for the
case CRP =3 (CRRA = 2). Although not having access to the hedging asset (with zero excess
return) does not have a direct effect on the expected evolution of total wealth, it leaves
the consumer subject to additional now unhedgeable risk calling for additional
precautionary savings. It is clear from panel (a) that initial consumption has to drop in
favor of consumption at later times. This effect is larger for larger degrees of prudence,
from Eq. (14). Panel (b) shows optimal consumption as a share of total wealth. If oil
price risk cannot be hedged due to incomplete markets or investment prohibitions, the
share of consumption in total wealth is no longer constant.

<h>PORTFOLIO ALLOCATION AND SPENDING WITH ENDOGENOUS OIL EXTRACTION</h>
----------------------------------------------------------------

The optimal speed of extracting oil may be understood using the Hotelling rule. This
states that the expected capital gains from keeping an additional barrel of oil in the
ground must equal the return from extracting, selling and earning interest on it
(Hotelling, 1931). We now extend this rule for volatile oil and financial asset prices.

<hs>  Optimal rates of oil extraction</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Eq. (20) indicates that the optimal rate of oil extraction is positively correlated with
the oil price, so that a sudden jump in the oil price requires a jump in the extraction
rate to make the most of it. Oil price shocks affect the rate of extraction most when
reserves (and in turn O) are highest, since this is when the majority of oil remains
exposed to volatile prices. As the date of exhaustion approaches, the rate of oil
extraction gets closer to what it would be without volatile oil and asset prices. Note
that the size of the fund does not matter for the optimal rate of oil extraction, only the
properties of the assets in the background.

<hs>  Sovereign wealth funds with endogenous rates of oil extraction</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As the asset allocation and consumption problems can be expressed in terms of total wealth
(22), propositions 2 and 3 apply. Judicious management of the fund allows consumption to
be smoothed in line with the permanent income hypothesis and to buffer consumption from
oil price volatility by hedging it with traded financial assets.

<h>POLICY IMPLICATIONS: NORWAY’S GOVERNMENT PENSION FUND GLOBAL</h>
------------------------------------------------------------

The policies of Norway’s Government Pension Fund Global (GPFG) 28 closely follow standard
CAPM recommendations ignoring oil wealth. Firstly, the GPFG uses the FTSE Global All Cap
Index as the equity benchmark (with around 7,400 individual stocks, a close approximation
of the market).29 This is consistent with holding the optimal risky (or market) portfolio
in (8) if W = F instead of W = F + V. Secondly, the Ministry of Finance chooses the
equity/bond mix, and in 2007 moved from 40/60% to 60/40%, as it was willing to accept more
risk for a higher return. This is consistent with choosing the size of the risky portfolio
based on preferences and the overall risk and return of the market, as in (9) with W=F.
Thirdly, a fixed share of the fund (4% according to Norway’s handlingsregelen) is consumed
each year, as in (12) with W=F. GPFG’s management mandate does not mention oil wealth at
all (NBIM, 2013), thus leaving Norway exposed to its large and volatile stock of oil
wealth: the “elephant in the ground”.30 Norway, and other oil-rich countries with similar
funds, would benefit by letting the asset allocation and the consumption rule in the GPFG
vary over time. Norway’s asset allocation should vary over time to hedge as much of the
volatility of remaining subsoil oil as possible.31 In the first-best case described in
Section 3 this would involve taking large long positions in some industries, and large
short positions in others (that may exceed the size of the fund), and reversing these
positions as oil is extracted. Such highly leveraged positions expose the country to
substantial risk if there are systematic shocks (Das and Uppal, 2004). They may also
become illiquid, which invalidates the assumption of exogenous prices. Furthermore, the
short positions assume that the covariance matrix is stable over time. In practice
correlations between oil and each sector vary depending on the type of shock hitting the
world economy (Kilian, 2009). As these correlations can only be estimated using past data
and the size of the hedging positions are so large, there is the potential for large basis
risk between oil and the hedging portfolio. Finally, as oil is extracted the highly
leveraged positions must be reversed which will incur substantial transaction costs for a
large fund.32 Therefore the target index should not be rebalanced too frequently and
portfolios should only be adjusted gradually. A more pragmatic, second-best approach to
asset allocation might be to only vary the equity/bonds mix.33 This would be transparent
and easy to explain to investors and the public. It would also notrequire short positions,
have lower transaction costs, and would not rely on a large, time-varying correlation
matrix covering all market assets. In this approach, the only risky asset is the overall
equity market (e.g., the FTSE Global All Cap Index). If oil is sufficiently positively
correlated with this market, the hedging demand to offset oil risk will exceed the
leverage demand.34 In this case, the GPFG should hedge the exposure of subsoil reserves to
oil price risk by holding fewer equities and more safe assets while there is oil in the
ground. Over time the oil reserves will be depleted and the exposure to equities embodied
in subsoil oil will fall. This allows the above ground fund’s equity exposure to rise, so
that equities make up a greater share of the portfolio as oil is extracted. The
consumption rule should be a constant share of total assets, and thus should fall as a
share of the fund as oil is extracted. If oil price risk is perfectly hedged as described
in Section 3, this rule should hold exactly. If hedging is imperfect, as would happen by
only varying the equity/bond mix, slightly more precautionary savings would be needed.
More precautionary saving is also needed if the fund faces a short-sales constraint.
Recently, the fund has stopped investing in coal and oil stocks. If the aim is to hedge
subsoil oil, it should go further by taking short positions in oil, gas and other stocks
that are positively correlated with oil prices. If the aim is to protect the environment,
spending should be curtailed to build up a buffer against less diversified risks. In
general though, spending as a share of the fund should fall over time as above-ground
assets account for an increasing share of total wealth. These recommendations are relevant
for the current debate in Norway. The fund excludes investments in certain assets for
social and political reasons, such as tobacco and defense firms, and early 2015 also in
assets affected by climate change and other environmental concerns such as coal, oil
sands, cement and gold mining. In late 2014 Norway also established a government
commission to assess its 4% spending rule due to concerns about excessive fiscal stimulus
(Ministry of Finance 2014b). This follows declining spending as a share of GPFG assets,
from nearly 6% in 2010 to below 3% in 2014, and there have been calls to limit spending to
3% in the future (Olsen, 2014).

<h>CONCLUDING REMARKS</h>
------------------

Commodity exporters have two major types of national assets: natural resources below the
ground and a sovereign wealth fund above it. Although some attempts to hedge commodity
price volatility have been made, from long-term forward agreements in iron ore until 2010
to the purchase of oil options by Mexico in 2008, there is no evidence of systematic
coordination of below- and above-ground assets. We have made the case for coordinating the
management of these two types of asset by integrating the theories of portfolio
allocation, precautionary saving, and optimal oil extraction under oil and asset price
volatility. Our main findings are as follows. Firstly, commodity exporters should change
the allocation of their sovereign wealth fund by leveraging all risky assets and hedging
subsoil oil risk. These effects are proportional to the ratio of oil and fund wealth, so
unwind as resource reserves are depleted. Secondly, consumption should be a constant share
of total oil and fund wealth. This stabilizes the mean and variance of spending as total
wealth evolves steadily whilst oil reserves are replaced by financial assets, but relies
on the degree to which the oil price can be hedged by components of the above-ground
portfolio. Thirdly, if oil wealth cannot be adequately hedged, less should be consumed
initially in the interests of precautionary savings in the face of the additional
unhedgeable risk that remains. Fourthly, the rate of oil extraction should be faster than
predicted by the standard Hotelling rule if oil prices are volatile and positively
correlated with financial markets. This generates a risk premium on subsoil oil, as convex
extraction costs will fall faster than the rate of extraction. The size of the premium
will depend on oil’s correlation with the market, and disappears to zero if their returns
are independent. Our analysis attempts to offer a first step towards an integrated
approach to managing sovereign wealth funds and natural resources under uncertainty. To do
this we combine canonical models of asset allocation, precautionary savings and oil
extraction. These models, while widely used and theoretically appealing, have received
empirical criticism (Griffin, 1985; Jones, 1990; Fama and French, 2004; Anderson at al.,
2014). Future work can address this along three dimensions. The first is to analyze the
effect of financial assets on natural resources in more detail, allowing for the
exploration and discovery of new reserves35, and extraction decisions at the discrete well
level (Kellogg, 2014; Anderson, et al., 2014; Venables, 2014). The second is to extend the
analysis to include other non-financial assets such as domestic non-traded capital, human
capital and pension liabilities, absorption constraints, general equilibrium effects of
spending resource revenues,36 and the benefits from structural reform to make the economy
less vulnerable to commodity price volatility. Finally, there is scope for modelling oil
and asset prices in more detail. In practice prices exhibit mean reversion (Wachter,
2002), stochastic volatility (Chacko and Viceira, 2005; Fouque et al., 2013), large jumps
(Ngwira and Gerrard, 2007) and time-varying correlations (Bollerslev et al., 1988; Longin
and Solnik, 1995). Although these extensions allow a better empirical testing of our
results, we conjecture that the qualitative nature of our policy insights will be
unaffected.


<h>REFERENCES</h>
----------

  [2] Ton S. Van Den Bremer, Frederick Van Der Ploeg. Managing and harnessing volatile oil windfalls. doi:10.1057/imfer.2013.4
  [4] George Chacko, Luis M. Viceira. Dynamic consumption and portfolio choice with stochastic volatility in incomplete markets. doi:10.1093/rfs/hhi035
  [5] David Chambers, Elroy Dimson, Antti Ilmanen. The norway model. doi:10.3905/jpm.2012.38.2.067
  [7] Sanjiv Ranjan Das, Raman Uppal. Systemic risk and international portfolio choice. doi:10.1111/j.1540-6261.2004.00717.x
  [10] Eugene F. Fama, Kenneth R. French. The Capital Asset Pricing Model: Theory and evidence. doi:10.1257/0895330042162430
  [13] Nicolae Gârleanu, Lasse Heje Pedersen. Dynamic Trading with Predictable Returns and Transaction Costs. doi:10.1111/jofi.12080
  [15] Viral V. Acharya, Lasse Heje Pedersen. Asset pricing with liquidity risk. doi:10.1016/j.jfineco.2004.06.007
  [16] James M. Griffin. OPEC behavior: A test of alternative hypotheses
  [21] Ryan Kellogg. The effect of uncertainty on investment: Evidence from texas oil drilling. doi:10.1257/aer.104.6.1698
  [23] Lutz Kilian. Not all oil price shocks are alike: Disentangling demand and supply shocks in the crude oil market. doi:10.1257/aer.99.3.1053
  [25] Erling Røed Larsen. Are rich countries immune to the resource curse? Evidence from Norway's management of its oil riches. doi:10.1016/j.resourpol.2004.12.001
  [26] Hayne E. Leland. Saving and uncertainty: The precautionary demand for saving. doi:10.2307/1879518
  [27] François Longin, Bruno Solnik. Is the correlation in international equity returns constant: 1960-1990?. doi:10.1016/0261-5606(94)00001-H
  [28] Robert C. Merton. Optimum consumption and portfolio rules in a continuous-time model. doi:10.1016/0022-0531(71)90038-X
  [32] Bernard Ngwira, Russell Gerrard. Stochastic pension fund control in the presence of Poisson jumps. doi:10.1016/j.insmatheco.2006.05.002
  [36] Robert S. Pindyck. Uncertainty in the theory of renewable resource markets. doi:10.2307/2297693
  [37] A. Sandmo. The effect of uncertainty on saving decisions. doi:10.2307/2296725
  [42] Jessica A. Wachter. Portfolio and consumption decisions under mean-reverting returns: An exact solution for complete markets. doi:10.2307/3594995
  [43] Stephen P. Zeldes. Optimal consumption with stochastic income: Deviations from certainty equivalence. doi:10.2307/2937848
<ART>The effects of access to health insurance: Evidence from a regression discontinuity design in Peru
================================================================================

Authors: Noelia Bernal, Miguel A. Carpio, Tobias J. Klein
DOI: 10.1016/j.jpubeco.2017.08.008
Year: 2017  |  Pages: 122-136
ASJC codes: 2002, 2003
Keywords: Health care utilization, Informal sector, Public health insurance, Regression discontinuity design, Supplier-induced demand

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

In many countries large parts of the population do not have access to health insurance. Peru has made an effort to change this in the early 2000s. The institutional setup gives rise to the rare opportunity to study the effects of health insurance coverage exploiting a sharp regression discontinuity design. We find large effects on utilization that are most pronounced for the provision of curative care. Individuals seeing a doctor leads to increased awareness about health problems and generates a potentially desirable form of supplier-induced demand: they decide to pay themselves for services that are in short supply.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

In developing countries, a large number of individuals is not covered by health insurance
(Banerjee et al., 2004; Banerjee and Duflo, 2007). The reasons for this are manifold. On
the one hand, individuals are often used to relying on informal forms of risk-sharing
instead of being covered by formal health insurance and therefore do not demand
insurance.2 On the other hand, it has in the past not been seen as the role of the
government to provide health insurance. Moreover, the World Health Organization and the
World Bank stress that, even when there is public health insurance, it often does not
reach large parts of the population and especially not the poorest families because it is
only provided to the minority of employees in the formal sector (WHO, 2010; Hsiao and
Shaw, 2007). For instance, until the late 1990s, only 23% of the individuals in Peru had
health insurance (CEPLAN, 2011). This may be a cause of concern, because health insurance
does not only protect individuals against catastrophically high health expenditures
(Wagstaff and Doorslaer, 2003). It also encourages them to see a doctor instead of simply
buying medication, and thereby promotes appropriate treatment of illnesses that is often
argued to be absent (Commission on Macroeconomics and Health, 2001; International Labour
Office et al., 2006). In reaction, many low and middle income countries have recently
introduced Social Health Insurance (SHI) targeted to the poor, with the goal to improve
their health and also to provide them with protection against the financial consequences
of health shocks. Coverage by SHI may or may not be free and typically means that
individuals receive medical attention from a service provider. The costs are usually paid
out of a designated government budget that is completely or partially funded by taxes.
However, to date, it is not well understood through which channels health insurance
coverage contributes to the well-being of individuals and how this relates to the
incentives provided to health care providers and patients and, more generally, to the
institutional environment.3 Important questions in this context are to what extent it is
possible to encourage individuals to seek medical attention rather than simply buying
medication in a pharmacy, how they can be motivated to invest into preventive care, and
what the effects of medical attention are on care consumption and out-of-pocket spending.4
Answering those questions is challenging for at least two reasons. First, we lack detailed
data on health care utilization and out-of-pocket expenditures, and second, it is
challenging to control for selection into insurance. The second problem means that a
regression of utilization or expenditure measures on insurance coverage will yield biased
results and will not estimate the causal effects of health insurance. In this paper, we
make progress in both directions. We use unusually rich data from the National Household
Survey of Peru (“Encuesta Nacional de Hogares”, ENAHO) to evaluate the impact of access to
the Peruvian SHI called “Seguro Integral de Salud” (SIS) for individuals outside the
formal labor market on a variety of measures for health care utilization and out-of-pocket
expenditures. We account for selection by exploiting a sharp regression discontinuity
design. The Peruvian case is interesting because SIS resembles Western public health
insurance systems and private insurance products in that it covers health care
expenditures related to both curative use and preventive care, but does not provide extra
incentives to invest in preventive care. Coverage is free for eligible individuals, and
those who are not covered by SIS typically lack insurance coverage.5 SIS was created in
2001 and subsequently reformed. Prima facie, these reforms have been successful, as
coverage by SIS is comprehensive and the fraction of the population making use of it has
increased from 20% in 2006 to 45% of the total population in 2011, reaching a relatively
high rate among the SHI programs in low and middle income countries (Acharya et al.,
2013). Yet, even though aggregate data suggest that some health outcomes improved since
the program has been implemented—between 2000 and 2010 total maternal mortality rates
decreased from 185 to 93 per 100,000 children born and child mortality rates decreased
from 33 to 17 per 1000 children born6—to date there is little evidence on the effects of
insurance coverage that is based on micro level data. A notable exception is the paper by
Neelsen and O’Donnell (2017) who study the effects of introducing SIS by means of a
differences-in-differences analysis.7 In this paper, we instead study the effects of an
upgraded version of the program and make use of the opportunity to control for selection
by exploiting the institutional setup in Peru that gives rise to a sharp regression
discontinuity design (RDD). It originates in a reform that was agreed upon in 2009. Since
the end of 2010, an individual who is not formally employed is eligible for free public
health insurance if a welfare index called Household Targeting Index (“Índice de
Focalización de Hogares”, IFH) that is calculated by Peruvian authorities from a number of
variables is below a specific threshold. We have access to this information and use it to
re-calculate the composite index of economic welfare. Variation in this index around the
threshold provides the natural experiment that we exploit. Two aspects of the
institutional background in combination with our research design are particularly
appealing. First, all individuals who are eligible for the program can be considered
covered by it. The reason for this is that enrollment is easy and quick, as it can take
place at the facility at which individuals seek treatment. It does not involve any fees,
and as individuals can usually receive free treatment within a few days, often on the next
day. Second, for our population of interest, crossing the eligibility threshold implies
coverage. This means that we will estimate the local average treatment effects of
insurance coverage for those individuals whose welfare index has a value close to the
eligibility threshold. The evidence we provide is policy-relevant, as it addresses the
question what would happen to individuals who are just not covered if eligibility would be
expanded by increasing the threshold. Making use of the rich data from the ENAHO of Peru
and the discontinuity generated by the institutional rules, we find large effects on
several measures of curative care use in combination with increases in out-of-pocket
spending. Individuals are more likely to receive medicines, it is more likely that a
medical analysis is performed, they are more likely to visit a hospital, and it is more
likely that they receive surgery. We shed light on the underlying mechanisms by
characterizing who pays for each of these forms of care. We show that the increased access
to doctors who perform medical analysis and prescribe medicines is usually fully financed
by SIS. At the same time, we find that medicines, hospital visits and/or surgeries are
financed by households themselves. In line with this, insurance coverage leads to
increases in out-of-pocket spending for medicines, hospital visits and/or surgery that are
likely driven by limitations faced by the health care suppliers. Using an estimator of
quantile treatment effects, we find that the effects on spending are particularly
pronounced in the top end of the distribution. We interpret these findings in more detail
by looking at them through the lens of a simple conceptual framework that we present in
Section 3 below. The main contribution of our paper is that we provide evidence in favor
of two arguments that are less common in economics.8 First, insurance coverage leads to
increased awareness about health problems, because it increases the likelihood that
individuals see a doctor; and second, this even generates a willingness to pay for
services that are not covered or not available, which in the context of Peru is a
potentially desirable form of supplier-induced demand. There is a huge literature on the
effects of health insurance coverage in the developed world. It is beyond the scope of
this paper to summarize this literature. Cutler and Zeckhauser (2000) provide an excellent
survey. One of the most important general findings is that more generous insurance
coverage leads to increases in health care utilization. This has been convincingly
documented in the context of the RAND Health Insurance Experiment (Newhouse, 1974, 1993;
Aron-Dine et al., 2013) and more recently in the context of the Oregon Health Insurance
Experiment (Finkelstein et al., 2012). In comparison, the literature on the effects of SHI
in low and middle income countries is scarce, but growing.9 The evidence points towards
large effects on utilization. At the same time, the picture is still blurred when it comes
to out-of-pocket spending. In part, this is because earlier contributions have not focused
on linking evidence on the effects on spending by type of care to the institutional
environment. Our data allow us to make progress in this direction and thereby shed light
on the underlying pathways. For Peru, Neelsen and O’Donnell (2017) find positive effects
of an earlier form of SIS on receipt of ambulatory care and medication, but no impact on
inpatient care and average out-of-pocket expenditures. Thornton et al. (2010) find that
initial take-up of subsidized, but for-pay insurance “Seguro Facultativo de Salud” among
informally employed individuals in Nicaragua was as low as 20%. Moreover, after the
subsidy expired most individuals who previously signed up cancelled their insurance. The
results for the few who did sign up and kept their insurance suggest that insurance could
have a positive effect in the sense that average health care expenditures, which are
generally seen as too low, increased. This could, however, also be the case because those
who bought insurance and kept it constitute a negative selection of risks for whom the
effect of insurance is particularly high. Next to this, there are a number of studies on
Mexico, including Barros (2008), King et al. (2009), Sosa-Rubi et al. (2009), and
Galárraga et al. (2010). All of them investigate the effects of the “Seguro Popular”
program, whose aim is—as the SIS's in Peru—to improve access to health insurance for the
poor. Unlike in the Peruvian, but like in the Nicaraguan program, coverage in the Mexican
program is not for free. The findings in all four papers consistently suggest that the
demand for medical care has shifted to providers that are part of the system, and in line
with this, individual health care expenditures have been reduced, including catastrophic
health expenditures. In that sense, the program was successful in being a transfer
program, but less so in encouraging individuals to seek care when ill. The findings do not
suggest that utilization has increased for types of care other than obstetric utilization.
Turning to China, Lu (2014) shows supplier-induced demand to be potentially important. She
finds that when doctors expect to obtain a proportion of patients' drug expenditures, then
they write more expensive prescriptions to insured patients. Wagstaff et al. (2009) find
that the launch of a heavily subsidized voluntary health insurance program in the rural
parts of the country led to increased outpatient and inpatient utilization, but has not
reduced out-of-pocket expenditures. In contrast, Wagstaff (2010) finds for Vietnam that
insurance coverage led to a reduction of out-of-pocket spending and no impact on
utilization. The design of the program in Georgia is very similar to the one in Peru.
However, and in contrast to our findings, Bauhoff et al. (2011) find no effect of
insurance coverage on utilization. They argue that the reason for this is that individuals
were not aware of being covered, or that there were administrative problems that caused
them to indeed not be covered, that they did not make use of the services because the
program did not cover drugs, and because the perceived quality of the services was low.
Therefore, it is not surprising that their findings are different from ours for Peru.
Next, turning to Colombia, and comparing the results to the ones in this paper for Peru,
it becomes clear that the effects of insurance coverage depend on the design of the
system. In Colombia, private insurers mainly receive a capitation fee and therefore have
incentives to increase preventive services on the one hand and to limit total medical
expenditures on the other. And indeed, Miller et al. (2013) mainly find effects on
preventive care. In Peru, SIS covers both preventive and curative services and doctors are
reimbursed on the basis of the treatments they provide. Hence, participating hospitals and
health care facilities do not have an incentive to discourage curative treatments or
medical procedures in favor of preventive services. This explains why in Peru most of the
effects are on curative use. Finally, two recent papers, Gruber et al. (2014) and
Limwattananon et al. (2015), investigate the effect of a large-scale increase in health
insurance coverage for the poor in Thailand. They find that the program had positive
effects on health care utilization, negative effects on out-of-pocket expenditures, and
negative effects on child mortality rates. These findings are similar to ours for Peru,
except that we find positive effects on health expenditures at the top end of the
distribution. Our explanation for this is that individuals, once covered, became aware of
additional health care needs and payed for some of them out-of-pocket. We proceed as
follows. Section 2 discusses the institutional background and provides details on the SIS
program. We present a conceptual framework—an informal sketch of a model of demand for
health insurance and health care utilization—in Section 3. In Section 4 we provide
information on our data and in Section 5 we describe the econometric approach. Results are
presented in Section 6. A number of robustness checks are conducted in Section 7. Section
8 concludes. Additional results are presented in an Online Appendix.

<hs>  Seguro Integral de Salud</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~

The public health insurance program “Seguro Integral de Salud” (SIS), whose effect we
study in this paper, was introduced in 2001. Its overarching goal is to improve access to
health care services for individuals who lack health insurance, giving priority to
vulnerable groups of the population who live in extreme poverty and are not formally
employed (Arróspide et al., 2009). The creation of SIS and subsequent reforms led to a
substantial increase of health insurance coverage over time. Bitrán and Asociados (2009)
and Francke (2013) provide interesting descriptive analyses of this increase and its
relevance within the Peruvian health system in general. Between 2006 and 2011 the fraction
of the population making use of services provided by SIS increased from 20 to 45%, which
means that by then SIS was the main health insurance provider in Peru.10

<hs>  Eligibility and benefit package</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The aim of the government was to target poor groups in the population. For this, ideally,
eligibility should be based on accurate information on income at the level of the
individual or family. However, such information is typically not available in developing
countries because a large part of the population works outside the formal sector and
therefore does not pay income taxes and social security contributions. Eligibility for SIS
is therefore based on the so-called Household Targeting System (“Sistema de Focalización
de Hogares”, SISFOH). A unified household registry is maintained and is used to calculate
targeting indicators at the level of the family.11 Data are collected by government
officials on a continuous basis and using a standardized form. There are questions on,
among other things, housing characteristics, asset possessions, human capital endowments
and other factors. The IFH index is the main eligibility criterion for the sample of non-
formally employed individuals we consider in this paper. It is a linear combination of the
variables in the household registry that takes on lower values for households that are
poorer. Eligibility for SIS is based on SISFOH in the capital Lima from 2011 on, and in
the rest of the country from 2012 on. Online Appendix F explains in detail how the IFH is
constructed, including the complete list of variables and their weights. Individuals are
eligible if it is below a regional-specific threshold.12 Importantly, whereas potential
beneficiaries intuit the importance of their answers to the questions of the government
official, they do not know how exactly the IFH index is calculated and what their cutoff
value for eligibility is. SISFOH does not inform households about the value of their index
and only provides the result of the eligibility evaluation. If eligible, individuals have
the possibility to enroll into SIS at a number of places, including the Ministry of Health
(“Ministerio de Salud”, MINSA) facilities. They are covered as soon as eligibility is
confirmed, which is usually a matter of days, often only one. Then, they receive the
health services that are offered at MINSA facilities and that are part of the benefit
package. In this sense, eligibility also means coverage.13 In urban areas, the eligibility
evaluation is valid for a period of 3 years (4 years in rural ones). This means in
practice that re-enrollment after a year is automatic provided that individuals are not
covered by another health insurance, individuals do not ask to be un-enrolled in the
meantime, an individual changes address, and provided that there is no evidence for fraud.
It is not related to the IFH index and in practice, exclusion of individuals after a
period of enrollment is very uncommon. SIS offers a comprehensive package of health care
benefits, composed of a basic plan of health benefits called PEAS and two supplementary
plans. The PEAS plan is based on a wide-ranging list of needs that any public and private
insurance plan (including SIS) must address, grouped in the following six categories:
healthy population (preventive care), obstetric and gynecological care, as well as care
related to pediatric conditions, neoplasm conditions, transmittable conditions and non-
transmittable conditions.14 There is an extensive list of benefits related to each listed
need. The plan covers ambulatory patient services, hospitalization and emergency care.
Table A.1 in Online Appendix B shows that PEAS covers 994 out of the 12,421 possible needs
listed in International Statistical Classification of Diseases and Related Health Problems
(ICD-10), that is, up to 8.0% of all possible needs.15 It is estimated that PEAS covers
65% of the total disease burden (Francke, 2013). Importantly, for individuals covered by
SIS, benefits included in PEAS cannot be subject to exclusions, waiting times or latent
periods.16 Moreover, there are no co-payments, coinsurance, deductibles, or similar
fees.17 PEAS includes theoretical limits to the number of times an individual can receive
each listed benefit. However, these limits are effectively annulled by the two SIS
supplementary plans. Individuals enrolled to SIS are automatically covered by these plans,
that is, they do not need to sign up to them nor to fulfill new requirements. The Regular
Supplementary Plan18 adds 1640 more needs to the PEAS list, that is, an additional 13.2%
of needs included in ICD-10 (see Table A.1). This plan includes a monetary limit by event
close to US$ 1875. 19 Next to this, the Extraordinary Coverage Supplementary Plan20 is
particularly generous as it allows SIS to go beyond the list of needs established by the
previous two plans in a discretionary way, and also beyond the established limits. This
supplementary plan states a new extremely generous monetary limit: costs for an individual
must not exceed 2.5% of the annual SIS budget. There is an application procedure to access
benefits using standardized forms. In sum, SIS covers more than 2634 needs (21.2% of needs
included in ICD-10) and, through supplementary plans, the stated limits are offset so that
SIS offers a very generous package of health care benefits.21

<hs>  Supply side</hs>
  ~~~~~~~~~~~

The Ministry of Health (MINSA) runs a network of health care centers and hospitals that
provides services to individuals covered by SIS. They also serve individuals who are not
covered by SIS, who pay for this themselves. Patients usually first visit a health care
center and are referred to a hospital when the health care center cannot provide a proper
diagnosis or treatment. Health care centers do however not act as gatekeepers. That is,
individuals can also directly visit a hospital. Each MINSA facility is reimbursed by SIS
on the basis of the treatments it provides. Reimbursement rates are based on estimates of
the variable costs plus a markup.22 There is no capitation fee and there are no extra
incentives to either limit curative care use or encourage investments in preventive care,
as it is the case in Colombia, for example. Importantly for our findings, some MINSA
facilities suffered from a number of substantial supply limitations.23 They originate in a
cut that SIS experienced in its budget, which in turn resulted in a failure to transfer
resources for reimbursement to MINSA facilities during the entire year of 2011. The
effects of those supply limitations are not systematically documented, but there is
evidence that in response, especially hospitals charged money for medicines and treatments
to insured patients.24 To counteract this, “SIS agents” were put in place, who are
supposed to ensure that hospitals stop this practice in later years.25 Besides, there has
been a shortage of dentists and ophthalmologists. The rate of odontologists per ten
thousand inhabitants is one of the lowest among all medical professionals (Giovanella et
al., 2012) and it is even lower when they work as providers for SIS (Defensoría del
Pueblo, 2013). In addition to that, at that time, only a small number of ophthalmologists
provides services to SIS participants, which in turn limits the use of ophthalmological
care. Only recently, after our study period, the National Ophthalmological Institute, the
largest provider in Peru, joined the list of SIS providers. In sum, even though SIS offers
a comprehensive package of health care benefits, supply limitations and institutional
problems related to the transfer of resources from SIS to MINSA facilities made some
medicines and treatments not fully available and free for the insured. It is an empirical
question how this affects care consumption and out-of-pocket expenditures. We turn to this
question in our analysis below.

<h>CONCEPTUAL FRAMEWORK</h>
--------------------

It is instructive to interpret our empirical results through the lens of a conceptual
framework. We provide a formal model complementing this framework in Online Appendix A.
The primary purpose of this framework is to discuss the implications the institutional
setup has on health care demand, with a focus on individuals not being aware of some of
their health care needs when they are not covered by health insurance. Without them seeing
a doctor individuals are aware of some health care needs, but not all. Sen (2002)
distinguishes in this context between “internal” and “external” views of health and
stresses that “the patient's internal assessment may be seriously limited by his or her
social experience”, such as seeing a doctor or not.26 Importantly, and in contrast to what
is common in developed countries, in Peru the individual can buy all drugs at the
pharmacy. That is, there are no prescription drugs. Therefore, the baseline case is that
she buys drugs at the pharmacy to treat the health care needs she is aware of and pays for
this herself. This has been common practice for a long time and may of course ultimately
have adverse effects on health. However, evidence on this is scarce (Laing et al., 2001).
Suppose now that the individual considers seeking professional care at some cost. Because
of the cost, she will only do so if the health care needs she is aware of are important
enough to her. She will be more inclined to do so when insured, because she will expect
that at least some treatments will be covered by the insurance once she visits a doctor.
Suppose she decides to visit the doctor and the treatment is indeed covered by insurance.
Then it could be that because of this she will consume more care than she would if she
would have to pay for it herself, which could be due to the fact that individuals are
liquidity-constrained and health insurance helps them pay for health care, or because of
moral hazard.27 The value associated to this generates an additional incentive to see a
doctor in the first place. Conversely, one reason not to visit a health care center is the
perception that—even though health insurance gives individuals access to doctors—this is
not valuable because advice obtained from them is often of low quality, and therefore
making use of insurance coverage is not worth its (opportunity) cost, including the time
it takes to register.28 An important additional effect is that once individuals visit a
doctor, he may make them aware of additional health care needs. This is a form of what has
been termed supplier-induced demand (McGuire, 2000). Strauss and Thomas (1998) argue that
this is an important potential determinant of health care expenditures in developing
countries. The additional care consumption may or may not be provided to them for free,
even though there are effectively no formal coverage limits. As we explain in Section 2.3
above, the reason for this is that some facilities suffered from severe supply
limitations. This could lead to patients paying for some treatments or buying drugs
elsewhere, for instance at a pharmacy. If this is the effect of insurance coverage, then,
as long as one thinks of doctors as not providing misinformation to patients, one can make
the argument that spending money reveals the preference of the individual for these
increased expenditures and that the supplier-induced demand is therefore beneficial to the
individual. To summarize the empirical predictions, we expect utilization to increase once
individuals are covered by health insurance, and out-of-pocket health care expenditures to
either increase (when individuals are made aware of many useful expenditures) or decrease
(when the majority of the treatments are provided by the health care facilities and the
overall out-of-pocket expenditures decrease because less money is spent at the pharmacy
and in health care centers together).

<h>DATA</h>
----

This paper uses cross-sectional data from the ENAHO household survey for the year 2011,
which is representative at the level of each of the 24 departments in Peru. It is the only
data set that provides the information needed to re-compute the IFH index and, at the same
time, on health care utilization, its financing and out-of-pocket expenditures.29 Online
Appendix D contains details on the way we define our outcome variables. Data are collected
using face-to-face interviews with one or more respondents per household, who are also
asked to provide information on the other household members. Online Appendix C describes
the interview procedure related to the health questions. In brief, the part of the survey
related to health has two branches. In the first branch, individuals are first asked
whether they experienced health problems and then what they did in response. In the second
branch, individuals are asked which health care services they used and then who paid for
it. This means that individuals may be asked twice whether they visited a doctor, for
instance. Importantly, the set of outcomes in the first branch is finer than in the second
branch, which is why information on the financing source is not available for all
variables we use in our analysis. Our data also contain information on the level of out-
of-pocket expenditures by financing source. We construct three mutually exclusive
categories for the financing source: 1) fully insured, if the individual indicates only a
governmental program or other insurance program as the financial source; 2) out-of-pocket,
if the individual points only at a member of her household or a member of other household
as the financial source; 3) partially insured, if the individual reports the financial
source by combining alternatives of the first and second categories. SIS is targeted to
individuals who work in the informal sector. For these individuals, the IFH index is the
most important criterion to determine eligibility. Therefore, for our analysis, we select
individuals that belong to a household in which no member is formally employed.30 This
group comprises approximately 60% of the entire sample. In 2011, almost one third of the
population lived in the Lima Province and half of Peru's Gross Domestic Product (GDP) was
generated there. For two reasons, we focus on individuals from that province. First, in
2011 the IFH targeting rule was only applied in this area, before this was gradually
extended to the rest of the country (Ministerio de Salud, 2011). In other parts of the
country and in later years it was less strictly applied. Second, the Lima Province is very
densely populated and therefore there are enough health care centers and medical
professionals so that we can exclude that either a large distance or absence of the staff
explain that individuals do not demand health care.31 This means, however, that our
results do not necessarily apply to the rest of the country. Our sample contains
information on 4161 individuals after the two exclusion criteria are applied. Tables A.4
through A.6 in Online Appendix E provide summary statistics for the full sample. In our
main analysis below we use a more local sample to carry out regressions and report our
estimate of the baseline level for each outcome along with our estimate of the effect of
insurance coverage. As described in Section 5 below, this baseline is the expected outcome
for individuals who are just not eligible for SIS. It is a more meaningful statistic than
the raw mean in our sample, because it is for the same group of individuals for whom we
estimate the effects by means of exploiting the RDD.

<h>ECONOMETRIC APPROACH</h>
--------------------

In this paper, we estimate the impact of SIS coverage on a host of variables
characterizing health care utilization and out-of-pocket expenditures. Based on the
institutional setup described in Section 2.2 we do this by means of a RDD using the IFH
index as the continuous forcing variable.32 An individual is eligible for public insurance
if she lives under poor conditions, which is measured at the household level. In the Lima
Province, the condition for this is that the IFH index is below or equal to a value of 55,
provided that both, water and electricity expenditures do not exceed 20 and 25 Soles,
respectively. Hence, provided that the condition on water and electricity expenditures
holds, we have a sharp RDD. The first assumption we need to make for our analysis is that
if no insurance or insurance would be assigned to everybody around the threshold, then the
respective distribution of the outcome conditional on the index would be smooth in the
index zi around zero.34 Then, β2 is indeed the effect of coverage. This assumption cannot
be tested directly and is therefore the main assumption we will make. As we have argued
before, the institutional rules suggest that it holds, as no other programs or rules are
based on this eligibility threshold. Moreover, this assumption is supported by further
evidence that we present in Section 7 below.35 The second assumption is that insurance
status is monotone in eligibility. This holds by construction, as we are facing a sharp
regression discontinuity design and therefore, changing from a value of the index slightly
higher than the threshold to a value lower than the threshold will directly make an
individual eligible for insurance coverage.36 The final, third assumption is an exclusion
restriction. It is that in a small neighborhood around the eligibility threshold, the
value of the index, zi, is independent of the outcomes, and in particular εi.37 It would
be violated if households would manipulate their answers to the government official in
order to influence the value of the IFH index. As discussed in Section 2 this is unlikely
to be the case. We nevertheless test for manipulation in Section 7.1. Under the same
assumptions, it is also possible to exploit the RDD and estimate quantile treatment
effects, as described in Frandsen et al. (2012). The underlying idea is straightforward.
Instead of an average, the quantile treatment effect is the change in, say, the median of
the distribution of an outcome that results from being covered by public health insurance.
Results are presented in Section 6.2. Before presenting the results, it is worth noting
that our econometric approach does not involve a “first stage”, as it is usually the case
in similar studies exploiting a regression discontinuity design. It is easiest to see this
by inspecting the estimation equation above. If individuals are anyway not eligible and
hence not covered by health insurance because of their water or electricity consumption,
then we will control for this.38 Consequently, β2 is the effect of becoming eligible due
to crossing the IFH eligibility threshold for all other individuals. As we have explained
above, given the institutional rules eligibility essentially implies coverage. Hence, this
is not only the effect of eligibility, but also the effect of coverage. This is as if the
first stage is one, which is always the case in a sharp regression discontinuity design
(Hahn et al., 2001). Alternatively, as we discuss in Section 7.7 below, our estimates can
be interpreted as intent-to-treat effects, or lower bounds of effect sizes.

<hs>  Health care utilization</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

We start by showing the relationship between the probability to receive curative care and
the IFH index in Fig. 1.39 Recall that higher values of the index indicate a higher level
of welfare. Individuals are covered by SIS when the index is below the eligibility
threshold. In the figure, we plot estimates of the probability to receive curative care
against the IFH index minus the eligibility threshold, which is why we expect the downward
jump of utilization at zero that we also observe in the figure. The interpretation is that
insurance coverage has a positive effect on the probability to consume curative care.
Next, Table 1 shows estimates of the effect of SIS on the utilization of a number of
health services, including the one in Fig. 1.40 These are local in the sense that we
select individuals with an IFH index that is at most 20 points away from the eligibility
threshold and, as described in Section 5 above, we control for the value of the index
separately to the left and to the right of the eligibility threshold. We also control for
age, gender, whether the head of the household is female, the number of household members,
and years of education. We also report respective baselines in the second column, which
are estimates of the mean outcome conditional on the IFH index being just above the
threshold so that individuals are just not covered by health insurance. The last three
columns use interactions between the financing source and the outcome variable. Here, we
make use of the fact that individuals report on both jointly. For instance, individuals
are asked whether they visited a doctor and then, if they say yes, whether the service
they received was fully covered by insurance, whether they paid part of it out-of-pocket,
or whether they paid everything out-of-pocket. This allows us to for instance construct
the joint outcome “went to the doctor and services received were fully insured”. Table A.7
in Online Appendix E shows the respective numbers of instances in our data. We start by
looking at more general forms of care, typically provided by easily accessible health care
centers. The first row shows that health insurance coverage has a positive effect on the
probability of visiting a doctor in the four weeks prior to the interview. It increases by
9 percentage points from a baseline of 30%(significant at the 10% level). This is driven
by fully insured doctor visits (6 percentage points at the 5% level of significance),
while the effect on doctor visits that individuals have to at least partially pay for is
not significantly different from zero. The second row shows that coverage also increases
the probability to receive medicines in the four weeks prior to the interview by 15
percentage points, from a baseline of 42%. In contrast to the effect on doctor visits,
most of the effect—10 percentage points—is related to medicines that individuals pay for
out-of-pocket. The third row shows that coverage increases the probability that medical
analysis is performed in the last four weeks, by 5 percentage points from a baseline that
is not significantly different from zero. More than half of this effect—3 percentage
points—is explained by fully covered access. As for doctor visits, the effect on the
probability of receiving medical analysis and at least partly paying for it is not
significantly different from zero. As described in Section 2.3, MINSA health care centers
provide only basic services. As for care provided by hospitals, health insurance coverage
leads to an 8 percentage points increase in the probability to be hospitalized or to
receive surgery, from a baseline of about 4%. The survey does not contain information on
the financing source for both separately, but for both together. The last column suggests
that households paid at least for part of this themselves. So far, these results suggest
that coverage lead to increased access to doctors who perform medical analysis and
prescribe drugs. While the increases in doctor visits and medical analysis are usually
fully financed by SIS, drugs, hospitalization and/or surgery are at least partly financed
by households themselves—even though these can actually be considered covered by insurance
(see Section 2.2). The discrepancy can be explained by the supply limitations we describe
in Section 2.3. The results presented here shed some more light on the underlying
mechanism. They suggest that individuals are not getting all the drugs they need at the
MINSA facilities and therefore, they go elsewhere to buy them, for instance at private
pharmacies.41 Table 1 also shows that health insurance coverage has no significant effects
on utilization of dental and ophthalmological care during the previous three months. This
can be explained by yet another supply limitation described in Section 2.3, namely the
shortage of dentists and ophthalmologists. Turning to care that is more likely of a
preventive nature, we generally find no significant effects. As we explain in Section 2,
the system does not provide extra incentives for that. In fact, the only significant
effect we find is on the probability to see a doctor to receive information on the
prevention of a sickness (preventive campaign), and this effect is actually negative. This
could be an indication of moral hazard, in the sense that patients invest less in their
health in case they are covered by health insurance. It is interesting to contrast these
results to the ones by Miller et al. (2013) for Colombia, where the system provides larger
incentives to invest in preventive care, as already discussed in Section 1. And indeed,
Miller et al. (2013) find stronger positive effects on preventive care. Overall, the
picture that emerges is that the effects of health insurance coverage are positive for
forms of care that are of a more general nature and can be provided by MINSA health care
centers at relatively low cost, such as doctor visits and medical analysis. We provide
evidence that these services are indeed free to the patient. We also find positive effects
on receiving medicines, hospitalization and surgery, but here it turns out that
individuals pay for these services themselves. This suggests that insurance coverage may
have positive effects on out-of-pocket expenditures. In Section 6.2 below we follow up on
this by estimating the effects on out-of-pocket spending by type of care. Peru is a
country in which poor individuals are accustomed to not receiving any professional
diagnosis and where drugs can also be bought in a pharmacy without a prescription.
Therefore, taken together, our findings point towards the expansion of the program being a
success in the sense that it had a positive effect on health care utilization, even if
this is at least partly paid for by the individuals themselves.

<hs>  Expenditures</hs>
  ~~~~~~~~~~~~

We argue in Section 3 that individual out-of-pocket spending could be positively affected
by health insurance coverage if receiving medical attention motivates individuals to
actually spend more on their health themselves, because they become aware of additional
health care needs. This positive effect could originate in, or be reinforced by the supply
side limitations described in Section 2.3. We have shown above that health insurance
coverage has positive effects on the likelihood that individuals receive medicines that
they pay for out-of-pocket, and also on the probability that they visit a hospital and/or
surgery is performed and that patients pay for out-of-pocket. Obviously, health insurance
coverage could also reduce out-of-pocket spending because individuals do not have to pay
for certain treatments anymore, or pay less. So, whether the overall effect is positive or
negative is an empirical question. In this section, we characterize the effect of health
insurance coverage on the full distribution of out-of-pocket spending and also perform an
analysis by spending category. Starting with mean spending, Fig. 2 suggests that total
out-of-pocket expenditures actually increased with insurance coverage. In Table 2, we use
a variety of outcome measures related to moments of the distribution of health
expenditures that have also been used in other studies.42 They either attempt to measure
expected health expenditures, their cross-sectional variability—interpreted as health
risk—, or the likelihood to incur catastrophic health expenditures.43 Table 2 presents the
results. The first dependent variable is an indicator for incurring at least some health
expenditures. We find no significant effect on this outcome, suggesting that health
expenditures are, if at all, mainly affected at the intensive margin. Turning to the
intensive margin, the second outcome is the level of annual health care expenditures. We
find that insurance coverage leads to an increase of annual spending by about 282 Soles on
average, which corresponds to 102 U.S. dollars, —in line with the idea that individuals
are motivated to spend more on their health when using medical services more often (which
they do according to Table 1 in the Online Appendix). This is about 1.5% of the average
household income among the insured (18,800 Soles according to Table A.4). The effect is
not significantly different from zero when we use log expenditures. With our next outcome
measure, we examine a possible effect on the variability of medical spending in the cross
section. It is the mean absolute deviation of health expenditures, calculated separately
by insurance status, and similar to the one used by Miller et al. (2013). Health insurance
has no significant effect on it. The fifth and sixth measures are constructed from
residuals obtained from a regression of health expenditures on the value of the index,
insurance status and the interaction of these two variables. Our aim is to measure the
variation of health care expenditures in a different way, and therefore we use the
absolute value and square of the residual instead of the more commonly used absolute value
of the expenditures and their square, respectively. Effects are significant at the 5 and
10% level, respectively. Looking at the results for the next two outcome measures, we find
significant effects on the probability that health expenditures exceed the median or the
75th percentile of the distribution of health expenditures in the entire population. In
order to control for possible income differences we also analyze the effect of insurance
on the share of annual health expenditures spent out-of-pocket at the individual level,
relative to the annual per capita household income. We find significant effects on the
expenditure shares and also on the absolute deviation of the share and the absolute value
of the residual of the share. For the last two outcomes in the second panel, we calculate
the 50th and 75th percentile of the distribution of the share and find that health
insurance increases the probability that this share exceeds the 50th and 75th percentile
by respectively 14 and 13 percentage points. Finally, we look into whether SIS changes the
probability of an individual incurring catastrophic health expenditures. Health
expenditures are defined to be catastrophic if the share of the expenditures relative to
per capita household income exceeds pre-defined threshold values. We follow Wagstaff and
Lindelow (2008) and use the thresholds 5, 10, 15, 20 and 25% for this. We find that the
probability that individual health expenditures exceed 5% of the per capita household
income increases by 12 percentage points, from a baseline of 20%. We also find highly
significant effects for higher cutoffs. Overall, the evidence presented in this section
and the previous one suggests that health insurance coverage has positive effects on the
level and the variability of out-of-pocket spending and that this is partly driven by
supply limitations that led to individuals paying for medicines, hospital visits and/or
receiving surgery. Fig. 3 complements this evidence with estimates of the quantiles of the
distribution of health expenditures with and without health insurance coverage. As
explained in Section 5, also these estimates are obtained exploiting the discontinuity at
the eligibility threshold.44 Interestingly, we find that insurance has only a positive
effect on the higher end of the distribution. It is remarkable that we never find a
significant negative effect on either expected health expenditures or measures of
variability or risk of high expenditures. Miller et al. (2013), in contrast, find for
Colombia that insurance lowers both mean inpatient medical spending and its variability.
Likewise, Limwattananon et al. (2015) find that health insurance coverage leads to a
decrease in out-of-pocket spending in Thailand. To see what drives this and whether some
types of spending were negatively affected, Table 3 reports estimates using the log of
spending plus 1 in different categories as the dependent variable so that the reported
effects are (approximately) average percentage changes in spending. Consistently with our
results shown in Table 1, we find that spending on medicines increased by approximately
55% on average and that spending on care provided by the hospital and/or receiving a
surgery increased by approximately 41%.45 In light of our discussion in Sections 2.2, 2.3
and 6.1 these results suggest that the out-of-pocket expenditures are driven by the fact
that individuals did not receive all medicines at the facilities and went elsewhere to buy
them, and had to pay for some services at the hospitals even though they were covered by
insurance. This seems to be mainly explained by supply limitations, in particular the
short provision of medicines and budget constraints faced for some hospitals. Rises in
health care expenditures as we find them are usually seen in a critical way, especially if
some treatments are formally covered but individuals have to nevertheless pay for them.
However, one may question whether this is justified here. On the one hand, this increase
in expenditures can be seen as an additional burden to the individuals, possibly also
increasing the variability of expenditures in the cross-section. On the other hand, the
alternative could also be that individuals are not treated at all because they are not
aware of their health care needs. In that sense the increase in spending for medicines as
well as hospital care and/or surgery could also be seen as a desirable consequence of
insurance coverage, which leads to increased accessibility, and thereby gives individuals
the idea of using medical services in response to being insured.46 Moreover, looking at it
in yet another way, some treatments are at least partly covered by SIS, or a complement to
it such as a doctor visit or a medical analysis is, so that the overall price of being
treated is generally lower, which means that the law of demand (that lower prices mean
more demand) would also predict an increase in usage. So also in that sense our findings
could be less worrying than they may first seem.

<h>SENSITIVITY ANALYSIS</h>
--------------------

In this section, after having presented the main results, we assess whether they are
sensitive to the particular specifications we have used, and whether the identifying
assumptions we have made can be supported by additional empirical evidence. We start by
examining whether households may have manipulated the IFH index in order to become
eligible for public insurance. Thereafter, second, we perform the analysis for a bigger
sample. Throughout the analysis, we have controlled for covariates. Therefore, third, we
also conduct the analysis without controlling for covariates and we assess whether there
were jumps in the expectations of covariates at the eligibility threshold. In passing, we
confirm that also the expectation of water and electricity consumption, respectively, do
not exhibit such a jump. Fourth, we assess whether there were discontinuities at other
values of the welfare index. This would raise concerns, as our approach builds on the
premise that there is only one discontinuity of the expected outcomes in the welfare
index, at least locally. After that, fifth, we conduct a non-parametric analysis. Sixth,
we assess whether the existence of other programs could challenge the validity of our
results. And finally, seventh, we discuss when our results could be considered lower
bounds of the effects of interest. All corresponding tables and figures can be found in
Online Appendix I.

<hs>  Manipulation of the running variable</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

A common threat to studies based on a RDD is the incentive to manipulate the running
variable. For this, individuals need information on how the IFH is calculated. Then, they
need to use this knowledge to manipulate their answers to the questions posed by the
government official in order to qualify for SIS. This is unlikely to be the case for two
reasons. First, even though the information on how the index is computed is, technically
speaking, public, it is not easy to obtain and process it. Second, the set of variables
included in the IFH construction are verified by the government officials and therefore
difficult to manipulate. We nevertheless analyze this potential thread using the McCrary
(2008) test. The idea is that if manipulation takes place, then the density of the running
variable will be discontinuous at the cutoff. In our context, the density function would
show many households barely qualifying for SIS, that is, to the left of the cutoff, and
fewer failing to qualify, that is, to the right of the cutoff. The formal procedure is
twofold: first, a finely gridded histogram is obtained and then this histogram is smoothed
with a local linear regression on each side of the cutoff.47 Fig. A.10 presents the
results. There is no evidence for a jump of the density at the eligibility threshold,
supporting the assumptions made in the main analysis.

<hs>  Analysis for the full sample</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our main results have been obtained under the assumption that expected outcomes are
approximately linear in the welfare index, separately to the left and the right of the
eligibility threshold. In order to alleviate the concern that this assumption is strong,
we have performed the analysis locally, selecting a sample of individuals for whom the
index is at most 20 points away from the threshold. In general, there is a tradeoff
between precision and bias, and using a bigger sample has the advantage that the precision
of our estimates may increase. Therefore it is interesting to also perform the analysis
for the full sample and to compare the results to the main ones reported above. The first
column of, respectively, Tables A.12 and A.13, shows the results. Comparing Table A.12 to
Table 1 we see that the magnitudes of the estimated effects are slightly lower when we use
the full sample while the precision increases. But qualitatively, the results are very
similar. Comparing Table A.13 to Tables 2 and 3 we find a similar pattern, with the
exception of the results on health expenditures as a share of income and catastrophic
health expenditures. For the full sample, the magnitude of the estimated effects decreases
by more than the standard errors and hence some of them are not found to be significantly
different from zero. Overall, the picture remains qualitatively and also quantitatively
the same: the effects on utilization are strongest, in particular for curative use, health
expenditures increase in terms of levels and variability, driven by increases in out-of-
pocket spending for medicines.

<hs>  Testing for discontinuities in household characteristics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

For our approach to be valid it is necessary that the covered and non-covered individuals
who have a value of the IFH index close to the eligibility threshold are similar to one
another (Section 5). It is standard practice to test whether the expectation of covariates
such as age or gender is a continuous function in the welfare index around the eligibility
threshold. When it is found not to be, then one may be concerned that the assumptions
underlying our analysis do not hold and one may want to conduct the analysis without
controlling for covariates. We first conduct both a graphical and a formal analysis in
which we replace the dependent health variables by the observed covariates gender, age,
years of education, the number of household members, and whether the woman is the head of
the household. These are the variables that we use as controls in order to be able to
obtain more precise estimates. We also tested for discontinuities in household income,
total household expenditure, and also water and electricity consumption. We would be
concerned if water and electricity consumption would exhibit a discontinuity because
eligibility is only based on the index if both of them are not big enough. Fig. A.8 and
Table A.14 summarize the results. The latter reports estimates of the effect of insurance
on these variables, conducted either at the household or at the individual level,
depending on the variable. We do not find evidence for discontinuities. We also conducted
the main analysis without controlling for covariates. Tables A.12 and A.13 show that
results are actually very similar and that the main conclusions we have drawn remain the
same.

<hs>  Jumps at non-discontinuity points</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our analysis implicitly assumes that the only discontinuities occur at the eligibility
threshold, 55, as we have specified conditional expectations to be linear in the forcing
variable, separately to the left and to the right of this threshold. A first way of
assessing this is to conduct a graphical inspection. Figs. A.2 through A.7 suggest that
the discontinuities do indeed mainly arise at the eligibility threshold. Besides,
following Imbens and Lemieux (2008) we conduct separate additional RDD analysis for the
samples of covered and non-covered individuals and use the midpoints of the index in the
respective samples as the threshold values. That is, we test for a discontinuity at values
of the index other than the actual threshold. Recall that in our main analysis we use only
individuals whose index is at most 20 points away from the eligibility threshold. Here, we
now use a sample of individuals with an index that is between 40 points lower than the
threshold and the threshold, and another sample of individuals for whom the index lies
between the eligibility threshold and 40 points above that. Results are presented in
Tables A.15 and A.16. In general, we observe no significant effects on health outcome
variables when we run the regressions using those hypothetical thresholds, with the
exception of a few cases.48 Figs. A.2 through A.7 suggest that what is picked up by this
robustness check is that the linearity assumption may be too strong for some outcomes. At
the same time, we find many more effects to be significantly different from zero when we
use the actual thresholds instead of the hypothetical ones. Next, we at least partially
address a related concern by carrying out a nonparametric analysis.

<hs>  Non-parametric analysis</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

To address the concern that linearity is too strong of an assumption even in smaller
subsamples we conduct a non-parametric analysis. For this we follow Calonico et al.
(2014). The main difference in terms of implementation is that we drop individuals for
whom either water or electricity consumption is too high to be eligible for health
insurance. Comparing the results reported in Tables A.17 through A.19 to the ones in
Tables 1 though 3 we again find that the strongest and most robust effects are on
receiving medicines and hospital care and/or surgery, financed out-of-pocket, and positive
effects on the level and the variability of out-of-pocket health care expenditures.

<hs>  Juntos and food aid program</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our identification strategy is based on the assumption that discontinuities at the
eligibility threshold can be attributed to SIS. There are some programs whose presence
could in principle challenge this assumption. One of them is Juntos, a conditional cash
transfer program. It combines a geographic targeting of the poorest districts with
individual targeting, based on the IFH index and the presence of children up to the age of
14. However, Juntos is a rural program and our study focuses on the Lima Province, and our
data confirm that no individual in the sample belongs to Juntos. Besides, there is a
number of food aid programs oriented to the poor. To be precise, they are oriented to
different groups of the population, such as mothers, children and school students. Our
data show that 29% of the individuals of our sample receive at least support from one of
them.49 Importantly, since these programs do not use SISFOH's targeting rules and in
particular not the IFH index, it is unlikely that a discontinuity at the eligibility
threshold can be attributed to them. Our finding in Section 7.3 that household
expenditures do not exhibit a discontinuity at the insurance threshold provides additional
support for this interpretation.

<hs>  Re-interpreting our results as intent-to-treat effects or lower bounds of the effect sizes</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In our analysis, we estimate the effect of becoming eligible for SIS due to crossing the
eligibility threshold. As we describe in Section 5, we control for ineligibility that is
due to other reasons and explain why we therefore face a sharp regression discontinuity
design and estimate the average effect of becoming eligible. We argue in the Introduction
and in Section 2.2 that this effect is essentially the effect of insurance coverage,
because enrolling involves filling in a form and if eligible, individuals can usually come
back the next day to receive treatment. It could nevertheless be that individuals do not
know whether or not they are actually covered by health insurance. This by itself would
not be a problem if they would always try to enroll and then learn that they are actually
not eligible. If they wrongly believe that they are not eligible and therefore do not even
try to enroll, then they may behave as if they are not covered by health insurance. Our
analysis, however, assumes that they are covered. Consequently, the effects we estimate
can be re-interpreted as intent-to-treat effects or lower bounds of effect sizes for those
who know that they are covered. To see this, suppose that among those individuals with a
value of the index that is very close to the threshold, 40% of the eligible individuals
believe that they are not eligible and therefore the effect of becoming eligible is zero
for them. The effect we then estimate is the intent-to-treat effect, which is a weighted
average of the zero effect for those 40% who wrongly believe that they are not covered and
the actual effect for the remaining 60% of the individuals. The intent-to-treat effect is
always of the same sign but smaller in magnitude than the actual effect for those who know
that they are eligible and in that sense we are estimating lower bounds of the effect
sizes.50,51

<h>CONCLUSIONS</h>
-----------

Until recently, large parts of the population in developing countries did not have access
to public health insurance. While it is commonly believed that the effects of health
insurance coverage are positive, opportunities to control for selection by exploiting
natural experiments or by conducting field experiments are rare, and therefore we still
lack empirical evidence on its impact on health care utilization and out-of-pocket
expenditures. Besides, it is not yet fully understood through which channels health
insurance coverage ultimately leads to better health outcomes and to what extent it is
possible to encourage individuals to invest into preventive care. In this paper, we use
rich survey data from Peru to study the effects of the large-scale social health insurance
program called “Seguro Integral de Salud” (SIS). The SIS program is targeted to poor
individuals working in the informal labor market. We make use of the institutional details
that give rise to a sharp regression discontinuity design. We estimate the effect of
insurance coverage on a wealth of measures for health care utilization and health
expenditures. We find strong effects of insurance coverage on arguably desirable, from a
social welfare point of view, treatments such as visiting a hospital and receiving surgery
and on forms of care that can be provided at relatively low cost, such as medical analysis
in the first place and receiving medication. Effects on preventive care are much less
pronounced. This is not surprising, as the system does not provide any extra incentives to
actually use them. Furthermore, we find positive effects of health insurance coverage on
the level and the variability of out-of-pocket spending that are mostly driven by
increased spending for medicines and for hospital care and/or surgery, resulting from
supply limitations. Based on this evidence, we develop two arguments that are less common
in economics. First, access to health care centers leads to increased awareness about
health problems. Once covered, individuals see a doctor and learn about the needs they
were unaware of. Second, this even generates a willingness to pay for services that are in
short supply, which in the context of Peru is a potentially desirable form of supplier-
induced demand. By spending out-of-pocket, individuals reveal their preference for medical
care. Overall, the evidence suggests that when compared to health care systems in other
developing countries, the Peruvian one is a notable exception. It seems to reach its goal
to provide access to medical care to a sizable fraction of the poor. A key determinant of
this success seems to be that the monetary cost of enrolling is zero, instead of being
small but positive, which it is elsewhere. As of now, there is no evidence on the effects
this will have on objectively measured health, but it is imaginable that increased access
will ultimately lead to better health outcomes.


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<ART>The extent and cyclicality of career changes: Evidence for the U.K.
===================================================================

Authors: Carlos Carrillo-Tudela, Bart Hobijn, Powen She, Ludo Visschers
DOI: 10.1016/j.euroecorev.2015.09.008
Year: 2016  |  Pages: 18-41
ASJC codes: 2002, 2003
Keywords: Labour market turnover, Occupational and industry mobility, Wage growth

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Using quarterly data for the U.K. from 1993 through 2012, we document that the extent of worker reallocation across occupations or industries (a career change, in the parlance of this paper) is high and procyclical. This holds true after controlling for workers' previous labour market status and for changes in the composition of who gets hired over the business cycle. Our evidence suggests that a large part of this reallocation reflect excess churning in the labour market. We also find that the majority of career changes come with wage increases. During the economic expansion wage increases were typically larger for those who change careers than for those who do not. During the recession this is not true for career changers who were hired from unemployment. Our evidence suggests that understanding career changes over the business cycle is important for explaining labour market flows and the cyclicality of wage growth.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

One of the most important functions of the labour market is to pair the right set of
workers with the right set of jobs. This assignment process, however, is slowed down by
frictions that impede the reallocation of labour resources. For example, moving costs, re-
training, learning about one׳s ability, information frictions about the location of
workers or jobs, among others, can be important barriers for efficient resource
reallocation. The result of these frictions is that we observe large concurrent flows of
workers changing jobs directly from employer-to-employer as well as through spells of
unemployment. As documented by Davis (1987) and Jolivet et al. (2006), among others, this
excess churning is a common feature of all labour markets in OECD countries. The extent of
reallocation is not necessarily constant over the business cycle. In one view, recessions
are times in which the labour market is “cleansed” by speeding up the reallocation of
workers, something that was prevented from occurring by frictions during the proceeding
expansions (See, for example, Lilien, 1982; Mortensen and Pissarides, 1994; Caballero and
Hammour, 1994; Groshen and Potter, 2003; Jaimovich and Siu, 2014). This view is appealing
because it provides a possible explanation for why unemployment is persistently high in
recessions. It simply takes workers time to switch, e.g., from jobs in industries and
occupations for which demand is in secular decline to jobs in growing segments of the
labour market. However, this is not the only view of the reallocative effects of
recessions. Barlevy (2002) argues that, since employment-to-employment transitions are
large and procyclical, economic expansions, rather than recessions, are times in which
labour resources tend to reallocate to better uses. In his view recessions have a
“sullying” rather than “cleansing” effect on reallocation. In this paper, we study two
specific dimensions of reallocation: occupational and sectoral mobility of workers. If
recessions have an important reallocative impact then occupational and sectoral mobility
of workers are likely to be two important channels through which this reallocation
occurs.1 In this context we interpret a career as a sequence of jobs a worker has in the
same industry and occupation. A career change is a case in which a worker changes employer
and starts a new job in either a different industry or occupation from the one he or she
was previously employed in. We focus on career changes in the U.K labour market over the
period from 1993 to 2012. The U.K. is an interesting country to look at for our purposes
because it has one of the most flexible labour markets in Europe and exhibits one of the
highest levels of worker turnover in the OECD (see Jolivet et al., 2006). This high level
of turnover suggests that the U.K. labour market facilitates reallocation at a higher rate
than those in other European countries. Fig. 1 shows the evolution of the U.K.
unemployment rate during the period that we study, from 1993 through 2013. It shows that
this period can be split up into four distinct episodes. The first episode is a period of
economic expansion until 2001, during which the unemployment rate declined by about 4
percentage points.2 The second is a period of slow growth following 2001, when the U.K.
economy skirted a recession and the unemployment rate blipped up marginally. The third
episode is the economic expansion from 2002 until the start of the Great Recession in
2008, in which the unemployment rate remained centered around 5%. Lastly, the Great
Recession and its aftermath make up the final episode. Fig. 1 shows that the unemployment
rate increased by 3 percentage points during that period. It is the number and rate of
industry and occupation changes, as well as the associated wage changes, in this final
episode that we compare with the earlier parts of our sample. For this, we use individual-
level data from the U.K. Quarterly Labour Force Survey. We present our evidence at two
levels of detail. In the first part of our analysis we focus on aggregate patterns and
uncover facts on (i) the extent of career changes in the labour market and (ii) how they
fluctuate over the business cycle. In the second part we look closer at individual-level
patterns that can shine a light on what drives these career changes. In this part we
document (i) who change careers, (ii) which industries and occupations they come from and
go to, and (iii) whether they do so at higher or lower wage gains than those who switch
employers but stay in the same career. Five main findings emerge from our analysis of the
U.K. Labour Force Survey. The extent of career changes is high: A worker who changes
employers has around a 50% chance of switching to another occupation or industry. The
rates of career changes are remarkably similar for those that change employers with or
without an intervening spell of non-employment. Career changes in large part reflect
excess churning in the labour market: the actual net mobility across industries and
occupations due to career switches only amounts to 10% and 15% of the overall flows
between occupations and industries respectively. This evidence on career mobility is in
line with Longhi and Taylor (2011) who, using the same data source as us, find that the
extent of occupational mobility in the U.K. is high.3 The U.K. is not an exception.
Industry and occupational mobility rates are also high in the United States (see Moscarini
and Thomsson, 2007; Moscarini and Vella, 2008; Kambourov and Manovskii, 2008; Hobijn,
2012, for example.) Career changes decrease in recessions: The total number of workers
that change careers and the probability of a career change are procyclical. Moreover, for
a worker, the probability of a career change is also procyclical, whether conditioning on
changing employers directly, or on experiencing an intervening spell of non-participation,
or a spell of unemployment. In this sense the cyclicality of career changes in the U.K. is
similar to that in the U.S. For the U.S. Murphy and Topel (1987), Carrillo-Tudela et al.
(2014), and Carrillo-Tudela and Visschers (2015) have all documented that the occupational
and industry mobility is procyclical.4 Moreover, just like in the U.S., excess churning in
the U.K. is the main driver of the cyclicality of overall mobility across occupations or
industries. This is because employer-to-employer transitions, that account for the bulk of
this churning, are procyclical. Moscarini and Thomsson (2007), Moscarini and Vella (2008)
and Kambourov and Manovskii (2008), document these dynamics for the U.S. labour market.
Characteristics of career changers: Career changes are more likely for (i) those workers
actively searching for a job, (ii) those that made voluntary transitions (i.e. those who
‘resigned׳ from jobs, or gave up for ‘family or personal reasons’, as opposed to those
that were made ‘redundant’ or ‘dismissed’) and (iii) those workers that work part-time or
as temps. Though models of on-the-job search with multiple job types (as in Pissarides,
1994; Akerlof et al., 1988; Barlevy, 2002; Menzio and Shi, 2011; Hagedorn and Manovskii,
2013; Moscarini and Postel-Vinay, 2013, among others) do not specifically focus on career
changes, and do not include a formal occupational or industry choice, they do imply that
quits are procyclical. Our evidence suggests that many of these quits in the U.K. result
in career switches. This is, however, not only the case for employment-to-employment
transitions. Career changes are also very common for hires out of non-employment. In terms
of underlying demographics, young workers and women are more prone to change careers than
their older and male counterparts. Even after accounting for these characteristics, the
propensity to change careers for workers that start a new job remains procyclical. Thus,
our results are not due to changes in the composition of who gets hired over the business
cycle. Career paths: Across occupations, career changes that involve an upgrade in the
skill level are more likely through direct employer-to-employer transitions. On the
contrary, career changes that involve a step down in skill level are more likely after
spells of non-employment. Further, career changes tend to move workers from routine to
non-routine employment. Our results also show that these movements did not accelerate
during the Great Recession. Wage changes upon career changes: The majority of career
changes come with wage increases and these wage increases tend to be bigger than for those
workers that change jobs but remain in the same career. The wage gains for those who got
hired out of unemployment and changed occupations fell during the recession and became
smaller than the wage gains of those who did not change occupations. Several studies have
linked wage gains to employer-to-employer transitions (Akerlof et al., 1988; Hagedorn and
Manovskii, 2013). Our evidence here suggests that such wage gains disproportionately get
realized by workers changing careers rather than continuing in the same one. These
findings provide evidence as to which theories would be able to best explain labour market
reallocation through occupational and industry mobility of workers. Our evidence shows
that outcomes for career changers are different from those who remain in the same career
when changing jobs. This suggests that understanding career changes over the business
cycle is important for explaining the cyclicality labour turnover and wage growth. Most
current models of labour turnover, like those that allow for on-the-job search mentioned
above, provide theories of why turnover is highly procyclical. Though these theories have
heterogenous jobs, none of them explicitly considers a career change decision. Recent
models, like Carrillo-Tudela et al. (2014) and Groes et al. (2015), do contain a career
change margin and help us better understand the incidence of career changes over the
business cycle and across the income distribution, respectively. Taken together, the facts
we document are consistent with the view that the Great Recession and its aftermath has
affected workers across a large set of industries and occupations, with a broad-based
shortfall in economic activity preventing workers from pursuing alternate careers at
substantial wage gains. In this sense, our results are consistent with the “sullying”
effect of recessions put forward by Barlevy (2002). Of course, career changes are only one
form of reallocation of labour and other resources. Thus, our results do not imply that
recessions have no cleansing effect at all but rather that such a cleansing is not
happening through worker reallocation across occupations and industries. This is
important, because it means we find little support in the U.K. data for recent theories of
job polarization (Jaimovich and Siu, 2014) that point to occupational mobility between
routine and non-routine jobs during recessions as the major driving force of the secular
decline in routine jobs. The rest of the paper is structured as follows. In the next
section we discuss the Quarterly U.K. Labour Force Survey, the definitions of the main
variables, as well as the level of aggregation of the industry and occupational
classifications that we use. In Section 3 we present the aggregate evidence and focus on
broad patterns in the level and cyclicality of career changes in the U.K. In Section 4 we
present individual-level evidence and discuss what it suggests about the reasons for
career switches. Finally, we end with a brief discussion of the theoretical implications
of the facts we document in Section 5.

<h>DATA</h>
----

The data we use are from the U.K. Quarterly Labour Force Survey (LFS) and cover the period
1993Q1–2012Q3. The LFS has a rotating panel structure, depicted in Fig. 2, in which
individuals that live on the sampled address are followed for a maximum of 5 quarters,
also referred to as waves. Each quarter, one-fifth of the sample of addresses is replaced
by an incoming rotation group, or cohort. From this sample, we consider all male workers
between 16 and 65 years of age and all female workers between 16 and 60 years of age with
an ongoing career.5 In each wave, the respondents provide information about, among other
things, their labour market status as well as their occupation and the industry they work
in if they are employed. If non-employed, they provide the occupation and industry of
their previous job.6 Because we are interested in those workers who switch employers and
potentially change careers, and because non-employed workers provide information on
previous employment, we need observations on workers only for two consecutive quarters.
Thus, we use the two-quarter (2Q) longitudinal sample of the LFS. Fig. 2 depicts two
quarters of this sample as long-dashed rectangles, labeled “2Q”. As can be seen from the
figure, because of the rotating panel structure and sample attrition, the 2Q sample is
smaller than the quarterly cross-section. It consists of about 60,000 individuals each
quarter.7 Occupation and industrial classifications: To code occupations, the U.K. LFS
uses the Standard Occupational Classification (SOC). The occupational coding system was
redefined in 2001, from the SOC 1990 to the SOC 2000, which was used until the end of
2010. A drawback of this revision is that the SOC 1990 and SOC 2000 are not fully
compatible. To reduce potential incompatibility errors we focus on mobility across 1-digit
or major occupational groups. These groups are listed in Table 1 for both the SOC 1990 and
SOC 2000. At this level of aggregation, the disagreement between the two SOC is of 26.5%.
The disagreement between the two classifications introduces a level shift in some of the
occupational series at the time of the switch from SOC 1990 to SOC 2000. To correct for
this shift, we adjust all 5-quarter centered moving average series by running an OLS
regression on the log of the corresponding series with respect to a linear time trend, the
log of output per worker and a dummy which takes a value of zero before 2000Q4, and one
after. We then use the coefficient estimate of the dummy variable (irrespectively if it
was significant or not) to adjust the series up to 2000Q4.8 To code industries, the U.K.
LFS uses the Standard Industrial Classification (SIC). In this case the U.K. LFS does
provide homogenised industry information for workers for the entire sample period based on
the SIC 1992.9 We focus on industrial mobility on broad industrial sectors, which roughly
corresponds to a one-digit aggregation level, with 17 categories displayed in Table 2.
Wage analysis: For the last part of our analysis, we also consider the change in wages
when workers switch occupations or industries. The wage measure we use is the self-
reported gross weekly earnings, deflated using the CPI. Individuals in the LFS only report
their wages in the first and fifth waves. These are depicted by the circles labeled “W” in
Fig. 2. Because they report their wages one year apart, we can calculate annual wage
growth for these workers. However, to do so requires us to follow these workers for the
full five quarters that they are in the LFS. This sample is known as the five-quarter
longitudinal sample and is depicted by the short-dashed rectangle labeled “5Q” in the
figure. This sample contains, on average, about 11,000 individuals. Using this sample we
condition the wage analysis on employer changes through employment, unemployment or
inactivity based only on uninterrupted spells.10 We aggregate all these transitions to
analyse the wage changes among all workers.

<hs>  Level and probability of career changes</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We record a career change when a worker changed employer and reported an occupation or
industry in the new job that is different from the occupation or industry reported in the
last job held. Then, what is flagged as a career change depends on the level of
aggregation of the occupation and industry classifications used. Because we use the major
occupation and industry classifications discussed above, the career changes we flag
capture a substantial change in the nature of a worker׳s job.11

<hs>  Net mobility</hs>
  ~~~~~~~~~~~~

Theories that emphasize the cleansing effect of recessions on the labour market emphasize
how downturns accelerate the shift in labour market resources from segments that are in
structural decline to those that are on a positive long-run trend. These are theories that
focus on the net mobility of workers across professions and sectors. To put this net
mobility in the context of the magnitude of overall flows in the labour market, we follow
Davis and Haltiwanger (1992) and analyze excess reallocation. That is, we quantify by how
much the total gross reallocation measured by the flows introduced in the previous
subsection exceeds the minimum flows needed to achieve the net shift in the observed
allocation of workers across occupations and industries.

<h>THE EXTENT AND CYCLICALITY OF CAREER CHANGES</h>
--------------------------------------------

In this section we investigate both the level as well as the cyclical fluctuations of the
incidence of career changes in the U.K. labour market. In the first subsection we focus on
the level and report long-run averages over our whole sample period. In the second
subsection we shift our focus to how the prevalence of career changes moves over the
business cycle.

<hs>  Long-run averages</hs>
  ~~~~~~~~~~~~~~~~~

The U.K. labour market displays a surprising degree of churning. Over our sample period,
the sum of career movers and stayers is on average 1.3 million per quarter. This amounts
to 4.5% of the U.K.׳s working age population. Of those who get hired and have a previous
career, 43% come directly from a previous employer, 29% are hired out of unemployment, and
29% were out of the labour force. These numbers are in line with Gomes (2012). What is
even more striking is the high share of these hires that involve a career change. Table 3
shows the average fraction of these hires that we classify as a career change. As can be
seen from the top row of the table, 49% of those workers with a previous career who start
a new job do so in a different (major) occupation from which they worked in before. This
fraction is even higher for industries, for which the majority, 53%, of such hires involve
a switch in major industry. The similarities in the extent of career changes across
occupations or industries arises mostly because the majority of career movers change
occupations and industries at the same time. For example, on average 75% of workers who
changed occupations also changed industries and 70% of workers who changed industries also
changed occupations. Though high, these numbers are in line with evidence for the United
States. For example, Carrillo-Tudela et al. (2014), using data from the Current Population
Survey, and Carrillo-Tudela and Visschers (2015), who rely on the Survey of Income and
Program Participation, both find that about half of the hires in the United States involve
a career change as well. One caveat is important to note. Reporting errors, more so for
occupations than for industries, are common in surveys like the U.K. LFS. If estimates
from other datasets are applied to our results for the U.K. LFS, then, maybe even as much
as a quarter, of the career moves that we measure could be due to workers misreporting
their occupation and/or industry in the survey.13 However, even if this is true, this
would still mean that about a third of all hires of persons with previous work experience
involves them changing either the industry or profession that they work in. Even after
such a drastic downward adjustment, this would imply that more than one percent of the
U.K. working age population switches careers every quarter. Rows 2 and up of Table 3 list
the probability of a career change conditional on the labour market status of the worker
in the quarter before she or he starts a new job. As can be seen from the table, the
average probability of a career change is around 50% for each of these types of hires. Two
groups of workers stand out as having a higher probability of switching careers than
others. The first consists of workers who make an EE transition and who actively searched
for the new position in the old job. These are more likely workers who actively pursue a
voluntary change in their career path. To be specific, career or job changes are
categorised as voluntary when workers report in the LFS that they left their previous
employer because they “resigned”, went to “education or training” or “gave up for family
or personal reasons”. Involuntary career or job changes are made by those workers who left
their last job because they were “dismissed”, “made redundant/took voluntary redundancy”,
“temporary job finished” and “gave up work for health reasons”. Finally, workers in the
other group are those who left their last job because they “took early retirement”,
“retired” and due to “other reasons”.14 Active search encompasses all activities that
involve the worker to contact or actively pursue job opportunities rather than browse job
opportunities that are available. This is the definition of job search that defines a
person without a job as being unemployed. The specific LFS answers that result in a person
being classified as an active searcher are listed in the Appendix. The second group of
workers with a higher probability of moving to a different career are those who were
unemployed for two quarters or more in the quarter before they started their new jobs.
These transitions most likely reflect involuntary career decisions that occur in long
spells of unemployment. Such career changes are often emphasized as driving up the natural
rate of unemployment in the short-run in the wake of a recession due to mismatch in the
labour market. Recent studies show that mismatch can only account for a small part of
overall fluctuations in the unemployment rate.15 Most studies of mismatch in the labour
market compare the composition of job openings by industry and occupation with the
composition of the pool of unemployed workers. This assumes that it is the pool of
unemployed workers that are required to make all the adjustments to make the skill
composition of the labour supply adjust to the composition of skills demanded. It turns
out that more than half of the workers that get hired out of unemployment end up making
such an adjustment. Moreover, our results suggest that the large number of EE career
switchers helps to accelerate this adjustment process. By providing a measure of the gap
between the skill requirements needed to fill the stock of job openings and the skill
composition of the pool of unemployed, measures of mismatch are a proxy for the net amount
of reallocation needed in the labour market to equilibrate the supply of and demand for
skills. However, gross mobility between careers far exceeds net mobility. The average net
mobility rates, nmt, over our sample period are 10% for occupations and 13% across
industries.16 This echoes the findings for the U.S. of Jovanovic and Moffitt (1990),
Kambourov and Manovskii (2008) and Auray et al. (2014), who show that net mobility
accounts for only a small proportion of gross mobility across industries and occupations.

<hs>  Cyclical fluctuations</hs>
  ~~~~~~~~~~~~~~~~~~~~~

Whether recession are times of accelerated or of relatively slow reallocation in the
labour market can, of course, not be gleaned from the long-run averages we reported so
far. To answer this question we now present evidence on the fluctuations, in deviation
from these averages, in the extent and probabilities of career changes over our sample
period. Above, we have focused on comparing the Great Recession with the previous episodes
in the data. The procyclicality of the level and probability of career changes that we
documented, however, is also robust to other ways of business cycle accounting. For
example, it also shows up if one uses the Hodrick and Prescott (1997) filter to
distinguish between trend and cycle in the unemployment rate and the time series plotted
in Figs. 3 and 4.19 One possible explanation for the procyclicality of the propensity to
change careers out of unemployment is the increased incidence of workers being recalled to
their previous job during downturns. For example, Fujita and Moscarini (2012) find that,
in the U.S., those workers that become unemployed after being permanently separated from
their previous jobs are much more likely to make an occupational change than those that
were on layoff and recalled within 3 months. However, in the UK such recall practice is
minimal and, hence, is thus not likely to affect the results presented here. What could be
more pertinent is that, on the supply side, those workers who get laid off in recessions
would first look for a job that is similar to the one they lost and only slowly broaden
their search.20 However, as Carrillo-Tudela et al. (2014) argue, workers take into account
that they may be less likely to start a particularly successful career path during a
recession, which reduces their incentives to change careers at any duration. On the labour
demand side, because of the increased size of the pool of unemployed workers in
recessions, employers would be more likely to find candidates that more closely match the
career profile they are looking for. Some studies, like Ravenna and Walsh (2012) and
Sedláček (2014), suggest that employers also get more selective in their hiring practices
during downturns. Such an increase in the pickiness of employers about who they hire in
downturns also affects the opportunities of those who are employed and are looking to
change jobs and pursue a different career. These effects could result in a decline in the
fraction of EE transitions that result in a switch in industry or occupation during
recessions, as can be seen from the long-dashed line in Fig. 4. Another way to gauge the
relative importance of these effects is to look at the fluctuations in net mobility, NM,
over the business cycle. Net mobility for both occupations and industries is plotted in
Fig. 5. If recessions had a major “cleansing” effect that resulted in a substantial shift
in workers from occupations and industries in secular decline to those for which demand is
booming, then net mobility would increase during the recession as well during the
subsequent recovery. This is because during the recovery workers would, gradually perhaps,
find jobs in careers different from those that they were in before. It is exactly this
slow adjustment during the recovery that is often pointed to as a source of the jobless
recoveries from the last three recessions in the U.S. (Groshen and Potter, 2003; Jaimovich
and Siu, 2014). However, as Fig. 5 shows, there is no such persistent spike in net
mobility. Net mobility briefly went up at the onset of the Great Recession, but then
declined to levels rather lower than typical values in the period 2001–2008Q1. While the
early rise coincided with the wave of layoffs described by Elsby and Smith (2010), by the
end of the recession net mobility rate had fallen deeply, however. From this low level,
net sectoral mobility started to increase again during the 2010–2011 recession, only
reaching pre-recession levels at the end of the second recession. The increase in net
mobility in 2010 and 2011 is mainly due to workers flowing towards services sectors. The
main contributors to this increase are all in the service sector (in order of importance):
(i) Real estate, renting and business activities; (ii) Health and social work; (iii)
Education; (iv) Wholesale and Retail Trade including Repairs; and (v) Transport, storage
and distribution. This evidence on net mobility, together with that on the level and
probability of career changes presented above, is in line with Barlevy׳s (2002)
interpretation of the role of business cycle for labour market dynamics, here for career
changes, rather than job changes. He argues that, because labour turnover is higher during
expansions than during downturns, the reallocation of labour market resources is
procyclical rather than countercyclical. Our interpretation of the above results is that,
in terms of worker reallocation across occupations and industries, recessions do not
appear to be times of accelerated labour market reallocation which is prevented from
happening during expansions due to frictions. Instead, in a recession, workers seem to
stay put in their respective occupations and industries when labour market opportunities
for them dry up during downturns.

<h>CAREER CHANGES: WHY, WHO, WHERE, AND AT WHAT WAGE GAINS?</h>
--------------------------------------------------------

In this section we dive into the details underlying these aggregates and use additional
information from the U.K. LFS to analyse the reasons for the career changes, who changes
careers, what they do before and after the career change, and how the change affects their
wages. This turns out to yield further evidence supportive of the “sullying effect” of
recessions through the lenses of career changes.

<hs>  Reasons for career change</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~

Unfortunately, the U.K. LFS survey does not directly ask respondents who take jobs in a
different occupation or industry about the specific reason for their career change.
However, some of the questions asked allow us to indirectly infer some of the potential
reasons. In particular, we revisit the questions we first focused on in Table 3. That is,
for those who move directly from one employer to another we consider whether this move was
voluntary and whether or not they had been actively searching for a job before they
switched. For those who were unemployed in the quarter before they started their new job,
we consider the duration of their unemployment spell in that quarter. Because EE flows
account for the bulk of the turnover in Fig. 3, we focus on the evidence for this
switchers first. Fig. 6 divides up the EE flows into movers and stayers and classifies
them by whether or not they made a voluntary EE switch, panels (a) and (c), and by whether
they were actively searching on the job before they made the switch, panels (b) and (d).
The first thing that stands out from the figure is that the bulk of EE transitions are
voluntary. Moreover, the vast majority of EE transitions is not the result of the worker
actively searching for another job but rather of the worker getting a job offer without
searching. We interpret these two facts as suggesting that a lot of job changes are
voluntary quits that could occur as result of employers contacting workers. Recent
evidence for the U.S. also shows that many workers get hired without ever reporting to be
actively looking for a job (see Topa et al., 2014; Carrillo-Tudela and Visschers, 2015,
for example). This contrasts with the common perception, as expressed in Jaimovich and Siu
(2014), that recessions are times of accelerated involuntary structural transformation.
During such times a large number of workers supposedly gets displaced from jobs that will
never come back and thus are forced to look for and take jobs in sectors and occupations
different from those they worked in before. One possible explanation for why the incidence
of career changes among hires out of unemployment does not spike in the recession is that
workers that get displaced from jobs that are in secular decline might decide to drop out
of the labour force rather than to switch careers. This is especially a concern in the
United States, where the labour force participation rate dropped by more than 3 percentage
points in the five years after the start of the Great Recession.22 Such flows to
inactivity, however, are not likely to be important in the U.K. where the labour force
participation rate actually increased between 2007 and 2012.

<hs>  Who changes careers?</hs>
  ~~~~~~~~~~~~~~~~~~~~

Of course, the discussion in the previous subsection focuses on the Great Recession versus
the rest of the sample. In addition, the evidence presented does not condition on other
factors that might be correlated with the variables used to proxy for different reasons
for a career change. Here we show that the procyclicality of the probability of career
changes, shown in Figs. 4 and 7, is statistically significant even if one considers the
whole sample and also corrects for factors that affect the probability of a career switch.
We do so by presenting Probit estimates derived from a model where the dependent variable
is whether or not the hire of a worker with previous work experience results in a career
change. The explanatory variables include a set of worker characteristics, properties of
the job the worker is hired in, and variables that proxy for the potential reasons for why
the worker changed careers or not. Because the availability of some of the variables
related to the reasons for the career change depends on the labour market status of the
worker before he or she accepted the new job, we present the Probit estimates not only for
all hires but also condition them on what labour market status the worker had in the
quarter before starting the new job. The estimation results are presented in Table 4.23 In
terms of the effects of human capital on the probability of a career change, we find that
age decreases the probability of a career change, suggesting the importance of on-the-job
human capital accumulation. Educational attainment, however, affects occupations and
industries differently. Across occupations, high and medium skilled workers have a higher
probability of a career change than low skilled workers (our reference category). Across
industries, we find that low skilled workers have a higher probability of a career change
than medium and high skilled workers. These results seem to arise from differences in the
impact of skill levels by employment status. Across occupations, it is only the unemployed
for which high and medium skilled workers have a higher probability of a career change.
Across industries, low skilled workers have a higher probability of changing career when
mobility is through employment or inactivity, but not through unemployment. Table 4 also
shows the effects of different types of job characteristics on the probability of a career
change. This probability increases if the worker obtains a part-time versus a full-time
job or if the worker obtains a temporary versus a permanent job.24 Women have a higher
probability of a career change than men. Furthermore, the larger the household someone is
part of, the less likely a person is to change careers. That is, Hm is lower for persons
who are married or cohabitate. It also decreases, although not significantly, in the
number of children. The Probit estimates also reaffirm the results found in Table 3 and
Figs. 3, 6, and 7. We find that for employed workers, career changes are more likely among
those employed workers that made voluntary EE transitions and among those that were
actively searching for a job (our baseline category with respect to all the search
channels). Unemployed workers are more likely to make career changes than employed (our
baseline category) or inactive workers, while a career change through unemployment is more
likely to occur at longer unemployment spells. Using individual-level data in the Probit
regression allows us to shine a more detailed light on search method workers employed to
find their new jobs and how it affects their chance of changing careers. In particular,
the explanatory variables listed in Rows 18 through 21 get at this.25 We find that those
workers who find jobs responding to ads are more likely to change careers than those who
find jobs through other means. Conditioning on the worker-, job-, and search-
characteristics does not erase the significance of the procyclicality of career changes.
This suggests that the business cycle movements in occupational and industry mobility of
workers are not the result of the composition of the group of workers with a previous
career that gets hired changing with the cycle. The higher sensitivity of occupational
switches compared to industry switches to the aggregate unemployment rate is offset by the
higher sensitivity of occupational mobility with respect to the regional component of the
unemployment rate, reported in Row 2 of Table 4. Taking the results of Rows 1 and 2 of
Table 4 together both occupational as well as industry mobility comove very significantly
with labour market conditions.

<hs>  Origins and destinations</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~

Another way to gauge the reasons for career switches is to consider what type of job in
which industry and occupation workers come from and what type of job they end up in. This
is what we explore in this subsection. We focus on three aspects of the origins and
destinations of career changers in our data. The first is whether the jobs are full- or
part-time. The second is what industry and occupation career changers come from and which
ones they go to. Finally, we refine the occupation analysis by considering whether the
occupations are routine or non-routine. Full- versus part-time jobs: So far, we have
documented that most career changes result from voluntary labour turnover and that the
share of career changes that is voluntary is procyclical. That is, during downturns a
higher fraction of career changes is involuntary (see Fig. 6). This cyclical behaviour of
voluntary career changes is mirrored by the extent to which occupational mobility results
in full- or part-time jobs. Career changes turn out to be an important mechanism through
which workers move between part-time and full-time jobs and, on net, contribute positively
to part-time and to full-time job flows.27 On average 65% of hires resulted in a full-time
job and 35% of hires resulted in a part-time job during the 1993–2007 period. These hires
are disproportionately people who change occupations.28 Career movers on average get a
full-time job in 60% and a part-time job in 40% of the time. For those that switch
directly between employers we know both their full-time status before and after they get
hired and can thus infer whether their full-time status changed when switching jobs. Using
these data, we find that on average 13% workers making an EE transition move from part-
time into full-time employment, while 7% move from full-time to part-time employment
during the 1993–2007 period. The bulk of changes in the full-time nature of work, in
either direction, involves a career change. Of those who moved from part-time into full-
time employment, 66% changed careers; while from those that moved from full-time to part-
time employment 59% changed careers. During the Great Recession, however, the incidence of
part-time work increased. On average 37% of hires now resulted in a part-time job, while
63% of hires resulted in a full-time job. Consistent with this, the net contribution of
career changes to part-time-to-full-time flows declined during the same period.29 Thus, if
we would consider part-time jobs to be typically less desirable than full-time jobs, then
the shift in the full-time/part-time composition of career movers׳ new jobs during the
recession reflects a relative worsening of outcomes associated with changing careers in
downturns and thus a deceleration of the pace with which workers move to higher quality
jobs during those periods. Note, however, that the shift in the full-time/part-time
composition is much less pronounced than the shift in terms of voluntary versus
involuntary turnover, depicted in Fig. 6. Industries and occupations: Above, we suggested
that transitions from part-time to full-time jobs are generally considered a step up the
job ladder while the reverse are considered a step down. To paint a more detailed picture
of the job ladders that career changers are on, we consider the origins and destinations
of their career moves here in terms of industry and occupation. We do so by constructing
industry and occupation transition matrices for workers׳ career changes. These matrices
provide useful information on the mobility patterns of workers as they shed light on the
potential importance of individual occupations or industries in driving overall mobility.
Table 5 shows the transition matrix for workers changing careers across occupations.30
This matrix shows that all occupations exhibit a high degree of mobility. The dark-shaded
cells list the fraction of hires that get hired in the same major occupation as they were
working in before. Looking at the numbers for all hires, labeled as “Total”, the
probability of a career change ranges from 61% for sales occupations to 32% for
professional occupations. Across occupations, however, we observe some clustering by skill
level. To show this, we group together those occupations that require similar skill
levels. This results in three groups of high-, medium-, and low-skilled occupations. The
first two groups consist of three major occupation codes and the last group consists of
two major occupation codes. Career changes within each of these groups are highlighted in
light grey as the block diagonal in the transition matrix. As can be seen, the transition
probabilities in the grey cells tend to be higher than those in the other cells. There are
two destination occupations that are notable exceptions to this pattern. First, a
substantial number of career changes out of high-skill occupations result in jobs in
“Clerical and administrative” jobs. Second, the miscellaneous ninth category absorbs a
large number of career switchers from middle-skilled jobs.31 Although we observe similar
non-diagonal probabilities between rows in the transition matrix, we also observe that
workers are more likely to stay within their skill category or move to the highest skill
category after an EE transition and more likely to move to a lower skill category through
a UE or IE transition.32 These patterns suggest that workers tend to move more often to
occupations that demand skills closer to the ones they can supply. However, conditional on
moving to a different skill category, workers are more likely to make career changes that
involve an upgrade in the skill level through direct EE transitions, while career changes
that involve a lower skill level are more likely through spells of non-employment. This
evidence reinforces the view that occupational mobility through EE transitions are more
likely to be voluntary career changes in which workers mostly pursue upward career moves,
while occupational mobility through non-employment are more likely to be involuntary
career changes. Routine and non-routine occupations: One particular type of occupational
mobility that has been emphasized in the recent literature is that between occupations
that involve routine and those that involve non-routine tasks. The distinction between
these two types of occupations is relevant for the “Polarization” hypothesis (see Autor,
2003, Acemoglu and Autor, 2011, Autor and Dorn, 2013, among others). This hypothesis is
that, over the last decades, job tasks that can be captured easily by a set of explicit of
simple instructions or rules, i.e. ‘routine tasks’, have been increasingly taken over by
computers and machines. As a result, employment in those occupations in which workers are
mainly executing routine tasks, summarily called ‘routine occupations’, has declined. In
its place, employment has risen at the bottom of the wage distribution, in occupations
that require physical labour, yet with tasks that cannot easily be captured in routines to
be automated. This includes simple service jobs that require physical eye–hand
coordination and physical navigation, typically under the heading ‘non-routine manual’
jobs. Employment has also risen higher in the wage distribution, where tasks require
knowledge acquisition and creative thinking, with jobs put under the ‘non-routine
cognitive’ header.33 Jaimovich and Siu (2014) argue that this secular process of job
polarization accelerates during recessions when many routine jobs are permanently
destroyed and workers in those jobs are forced to pursue other careers. In this way, they
claim, the cycle is actually the trend, since this type of job polarization during
recessions is not reversed during expansions. To consider whether job polarization is
happening in the U.K. labour market and to what extent it is reflected in workers
switching from careers in routine to non-routine occupations, we split up the post-2000
data by occupation into routine and non-routine occupations, following Acemoglu and Autor
(2011). The second column of Table 1 contains a marker that signifies which SOC 2000
occupations are classified in which category. Fig. 8 shows employment in routine
occupations as both a share of the working age population as well as of total employment.
The figure shows that the share of employment in ‘routine occupations’ has steadily
declined in the U.K., similar to that in the U.S. (Jaimovich and Siu, 2014). However,
there was no acceleration in this trend during the Great Recession, as the “trend-is-the-
cycle” hypothesis would suggest. In fact, using more formal regression-based techniques we
find no significant cyclical component in the routine share series plotted in Fig. 8. This
is in line with the evidence for the U.S. in Foote and Ryan (2014). Fig. 9 shows the time
series of career changes that result in a switch between routine and non-routine
occupations. The first thing that stands out from this figure is the excess churning we
already saw in terms of the net mobility measure in Fig. 5. The net change in routine
employment induced by these career switches is negative and contributes to the trend
decline shown in Fig. 8. Just like in the U.S. (Cortes et al., 2014) IE and UE flows
contribute the bulk of this net decline. Most importantly, however, is the observation
that the share of routine to non-routine career switches does not increase significantly
during the recession, indicating that, in terms of career switches, there is no evidence
that the long-run downward trend in the share of routine employment accelerates during
recessions. In fact, the overall turnover between these two categories of occupations
seems to have declined in the recession. Of course, the data in Fig. 9 only includes
workers who have been employed before at some point, and are hired again. This means that
adjustment in the overall level of routine employment could also come about by a
diminishing inflow into routine occupations by labour market entrants, and by an increased
outflow of retirees from these occupations is not visible in our statistics. Cortes et al.
(2014), for example, emphasize that such a cohort effect is an important driver behind the
trend decline in routine employment in the United States. However, the lack of a cyclical
pattern in Fig. 9 suggests that this cohort effect most likely also does not fluctuate a
lot over the business cycle. Thus, our analysis for the U.K. is supportive of the same
conclusion that Albanesi et al. (2013) draw for the U.S.; weakness in the labor market in
the Great Recession was shared by non-routine and routine occupations alike, did not
disproportionately affect routine occupations, nor did it accelerate the secular decline
in routine jobs.

<hs>  Wage gains</hs>
  ~~~~~~~~~~

Thus far, we have shown that career switches make up a substantial fraction labour market
turnover, and of voluntary turnover in particular. Recent theoretical (Hagedorn and
Manovskii, 2013) and empirical (Daly et al., 2012) studies have emphasized the importance
of voluntary turnover and employer-to-employer transitions for understanding the cyclical
behaviour of wage growth. Our data suggest that distinguishing between career switchers
and stayers would refine our understanding of wage growth over the business cycle even
more. To see why, consider Tables 6 and 7, which summarize the distribution of percent
real wage changes for job switchers, conditional on moving careers or staying in the same
career, for the whole sample as well as for the three main periods in our sample.34
Because we are interested in wage changes, our analysis only includes hires for which we
have data in waves 1 and 5 of the survey, depicted in Fig. 2. In particular, that means
that for workers who flow through unemployment, we only have wage changes for those with
an unemployment spell shorter than 4 quarters. Long-run perspective: Table 6 shows the
probability that the hire of a worker with previous work experience results in a wage
gain. The table lists this probability conditional on whether the hire involves a change
in career and on the level of the wage earned in the previous job, measured in terms of
the percentile of the wage distribution. The probability of a positive wage gain is much
higher for workers who earned a low wage in their previous jobs. More importantly, for
those workers this probability is also higher when they change careers than when they did
not. For workers making an above-median wage, however, the probability of obtaining a
positive wage growth when changing employer is closer to 30% but now is higher for those
who do not change careers. This suggests that a large part of the voluntary career
mobility through employer-to-employer moves that we document is workers moving up the job
ladder to progress their careers.35 Where Table 6 provides information about the sign of
the wage change, the columns for the “Whole sample” in Table 7 show the distribution of
the magnitude of wage changes.36 The first takeaway from this table is the large degree of
dispersion in wage growth that results from a change in employers. Below the 50th
percentile of each distribution, workers can experience large negative wage losses when
moving employers, while above the 50th percentile workers experience large wage gains.37
The most striking feature of the distributions shown in Table 7 is that the dispersion of
wage gains is larger for career movers than for career stayers. This also holds true when
we condition on whether the worker changed employers through an intervening spell of
unemployment or not. Relative to stayers those who changed careers have higher wage growth
at and above the 50th percentile of the wage growth distribution; while the opposite
happens below the 50th percentile. This evidence again supports our interpretation that
workers typically change careers for wage gains bigger than for those that stayed in the
same occupation. It might seem counterintuitive that career changes through unemployment
do tend to lead to positive wage gains that are larger than those obtained by unemployed
workers who will stay in the same career. However, this evidence is not inconsistent with
a theory in which these potentially larger wage gains can only be obtained after a costly
reallocation process which only becomes worthwhile after job prospects in the original
career have deteriorated sufficiently (see, for example, Carrillo-Tudela et al., 2014).
Cyclical patterns: The last six columns of Table 7 show how the distribution of wage
changes varies over different business cycle episodes in the U.K. labour market. Across
occupations and industries the wage growth distribution of those workers that change
careers through unemployment shifts down during the recession. The decrease is stronger
across occupations than industries. Further, the shift in the wage growth distribution of
those who changed occupations through unemployment is sufficiently big that their wage
gains are now below the wage gains of career stayers even at the 75th percentile of the
wage growth distribution. In contrast, the wage growth distribution of workers that
changed employers directly through an EE transition or those that changed employers
through unemployment but did not undertake a career change, do not seem to respond as much
to business cycle conditions.38 The evidence presented suggests that career changers have
a higher probability of a substantially large wage increase than career stayers. However,
during the recession the wage gains of occupational changers decrease to the point that,
for unemployed workers, these have become smaller than the wage gains from changing
employer in the same occupation. As argued, for example, in Carrillo-Tudela et al. (2014),
the decrease in the gains of reallocation can help explain the drop in the probability of
a career change during the recession, documented in Section 3.2. Thus, the procyclicality
of the incidence of career changes and the associated wage gains that we document suggest
that adding a career change margin to our models of labour market fluctuations will help
improve our understanding of the, not well-understood, link between unemployment, labour
turnover, and aggregate wage growth.39

<h>DISCUSSION AND CONCLUSION</h>
-------------------------

Overall, the patterns in the UK LFS suggest that in good times career changes imply a
chance to improve a worker׳s position in the labour market. In downturns the gains
associated with career changes appear to diminish. From a theory perspective one can build
on Carrillo-Tudela et al. (2014) and Wiczer (2013) to reconcile these patterns using a
framework that incorporates heterogeneity in labour market conditions, costly mobility
choices between labour markets (career changes) and business cycle shocks. In such a
framework, fluctuations in the expected net returns to a career change induce workers to
adjust their mobility choices. In downturns, when net returns are low, workers decide to
stay in their careers and wait for conditions to improve instead of changing to a new
occupation or industry. In such a framework two motives for job mobility can arise: (i)
workers may move to other jobs because their current employment conditions worsen while
outside opportunities stay the same; (ii) workers may move because outside opportunities
improve while current employment conditions are unaffected. Although both reasons may be
at work, they are not necessarily two sides of the same coin. Aggregate conditions may
interact differently with the idiosyncratic shocks to workers׳ current employment than
with the stochastic arrival of new employment opportunities in different occupations or
industries. In these models, adverse shocks to current employment could then generate
‘involuntary’ transitions, through which workers try to recover the loss of prospects in
their current job. Increased opportunities elsewhere could draw workers to ‘voluntarily’
change their jobs and careers. The ‘pull’ of the latter kind of opportunities can be
especially strong in booms, in line with the evidence presented in this paper; while the
mobility ‘push’ associated with the shocks behind ‘involuntary’ transitions could be
especially relevant in recessions. Taken together, career changes are different from other
hires in terms of their cyclicality, their associated (wage) gains and the cyclical
variations in these gains. Incorporating a career-mobility dimension in equilibrium
business cycle models of the labor market can be a promising direction to contribute to
our understanding of the overall behaviour of labour turnover and wage growth over the
business cycle, and could help guide better policy responses to business cycle
fluctuations.


<h>REFERENCES</h>
----------

  [1] Daron Acemoglu, David Autor. Skills, tasks and technologies: Implications for employment and earnings. doi:10.1016/S0169-7218(11)02410-5
  [6] Steven J. Davis. Fluctuations in the pace of labor reallocation. doi:10.1016/0167-2231(87)90013-3
  [7] Steven J. Davis, John Haltiwanger. Gross job creation, gross job destruction, and employment reallocation. doi:10.2307/2118365
  [8] Michael W.L. Elsby, Jennifer C. Smith. The great recession in the UK labour market: A transatlantic perspective. doi:10.1177/0027950110389756
  [13] Pedro Gomes. Labour market flows: Facts from the United Kingdom. doi:10.1016/j.labeco.2011.08.002
  [14] Fane Groes, Philipp Kircher, Iourii Manovskii. The U-shapes of occupational mobility. doi:10.1093/restud/rdu037
  [16] Marcus Hagedorn, Iourii Manovskii. Job selection and wages over the business cycle. doi:10.1257/aer.103.2.771
  [17] Robert J. Hodrick, Edward C. Prescott. Postwar U.S business cycles: An empirical investigation. doi:10.2307/2953682
  [19] Bart Hobijn, Ayşegül Şahin. Beveridge curve shifts across countries since the great recession. doi:10.1057/imfer.2013.18
  [22] Grégory Jolivet, Fabien Postel-Vinay, Jean Marc Robin. The empirical content of the job search model: Labor mobility and wage distributions in Europe and the US. doi:10.1016/j.euroecorev.2006.02.005
  [23] B. Jovanovic, R. Moffitt. An estimate of a sectoral model of labor mobility. doi:10.1086/261708
  [24] Gueorgui Kambourov, Iourii Manovskii. Rising occupational and industry mobility in the United States: 1968-97. doi:10.1111/j.1468-2354.2008.00473.x
  [27] Guido Menzio, Shouyong Shi. Efficient search on the job and the business cycle. doi:10.1086/660864
  [29] Dale T. Mortensen, Christopher A. Pissarides. Job creation and job destruction in the theory of unemployment. doi:10.2307/2297896
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  [32] Giuseppe Moscarini, Kaj Thomsson. Occupational and job mobility in the US. doi:10.1111/j.1467-9442.2007.00510.x
  [34] Christopher A. Pissarides. Search unemployment with on-the-job search. doi:10.2307/2297899
  [35] David H. Autor, Frank Levy, Richard J. Murnane. The skill content of recent technological change: An empirical exploration. doi:10.1162/003355303322552801
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  [41] Gadi Barlevy. The sullying effect of recessions. doi:10.1111/1467-937X.00198
<ART>The fiscal cost of weak governance: Evidence from teacher absence in India
==========================================================================

Authors: Karthik Muralidharan, Jishnu Das, Alaka Holla, Aakash Mohpal
DOI: 10.1016/j.jpubeco.2016.11.005
Year: 2017  |  Pages: 116-135
ASJC codes: 2002, 2003
Keywords: Education, Governance, India, Monitoring, State capacity, Teacher absence, Teacher absenteeism

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

The relative return to strategies that augment inputs versus those that reduce inefficiencies remains a key open question for education policy in low-income countries. Using a new nationally-representative panel dataset of schools across 1297 villages in India, we show that the large public investments in education over the past decade have led to substantial improvements in input-based measures of school quality, but only a modest reduction in inefficiency as measured by teacher absence. In our data, 23.6% of teachers were absent during unannounced school visits, and we estimate that the salary cost of unauthorized teacher absence is $1.5 billion/year. We find two robust correlations in the nationally-representative panel data that corroborate findings from smaller-scale experiments. First, reductions in student-teacher ratios are correlated with increased teacher absence. Second, increases in the frequency of school monitoring are strongly correlated with lower teacher absence. Using these results, we show that reducing inefficiencies by increasing the frequency of monitoring could be over ten times more cost effective at increasing the effective student-teacher ratio than hiring more teachers. Thus, policies that decrease the inefficiency of public education spending are likely to yield substantially higher marginal returns than those that augment inputs.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Determining the optimal level and composition of public education spending is a key policy
question in most low-income countries. Many education advocates believe that low-income
countries need substantial increases in public education spending to meet enrollment and
learning goals (UNESCO, 2014); others argue that public sector inefficiencies leave
considerable room for improvement within existing education budgets, and that fiscal
constraints make it imperative to improve the efficiency of public expenditure (World
Bank, 2010). However, the data to assess the relative importance of these contentions
remains sparse, in part, due to the difficulty in detecting and measuring inefficiencies
in public spending. In this paper, we study one striking measure of public sector
inefficiency - teacher absences - with panel data collected 7  years apart in India at a
time of sharp increases in education spending. A large portion of this increase was
accounted for by the salary cost of hiring teachers to reduce the student-teacher ratio in
public schools. As a policy alternative to hiring more teachers, we show that reducing
teacher absences by increasing school monitoring could be over ten times more cost
effective at reducing the effective student-teacher ratio (net of teacher absence). Thus,
while the default approach to improving education in low-income countries is input-
augmentation, our results suggest that investing in reducing inefficiencies may yield much
greater returns. India presents a particularly salient setting for our analysis. It has
the largest primary education system in the world, catering to over 200 million children.
Further, over the past decade, the Government of India has invested heavily in primary
education under the Sarva Shiksha Abhiyan (SSA) or “Education for All Campaign.” Partly
financed by a special education tax, this national program sought to correct historical
inattention to primary education and led to a substantial increase in annual spending on
primary education across several major categories of inputs including school
infrastructure, teacher quality, student-teacher ratios, and school feeding programs.1
However, the public education system in India also faces substantial governance challenges
that may limit the extent to which this additional spending translates into improved
education outcomes. Our indicator of systemic inefficiency - teacher absence - presents a
particularly striking indicator of weak governance. A nationally-representative study of
over 3000 public primary schools across 19 major Indian states found that over 25% of
teachers were absent from work on a typical working day in 2003 (Kremer et al., 2005).
Although administrative data from the government's official records suggest that SSA has
led to an improvement in various input-based measures of school quality, there is little
evidence on whether these investments have translated into improvements in education
system performance, both with respect to intermediate metrics such as teacher absence and
final outcomes such as test scores.2 Our study of this nationwide campaign to improve
school quality in India uses a new nationally-representative panel dataset of education
inputs and outcomes that we collected in 2010. We constructed this dataset by revisiting a
randomly-sampled subset of the villages originally surveyed in 2003 (see Kremer et al.
(2005)) and collecting detailed data on school facilities, teachers, community
participation, monitoring visits by officials, and teacher absence rates. Thus, in
addition to reporting updated estimates of teacher absence, and independently-measured
summary statistics on input-based measures of school quality, we are able to correlate
changes in input-based measures of school quality with changes in teacher absence. The
panel data help mitigate concerns arising from fixed unobserved heterogeneity at the
village-level, and let us study how the sharp increases in public education spending over
the last decade have affected school quality. We find significant improvements in almost
all input-based measures of school quality between 2003 and 2010. The fraction of schools
with toilets and electricity more than doubled, and the fraction serving mid-day meals
nearly quadrupled. There were significant increases in the fraction of schools with
drinking water, libraries, and a paved road nearby. The fraction of teachers with college
degrees increased by 41%, and student-teacher ratios (STR) fell by 16%. The fraction of
teachers not paid on time fell from 51 to 22%, and the fraction of teachers reporting the
existence of teacher recognition programs increased from 50 to 81%. Finally, the frequency
of school inspections and parent-teacher association (PTA) meetings increased
significantly. However, reductions in teacher absence rates were more modest. The all-
India weighted average teacher absence in rural areas fell from 26.3 to 23.6%. 3 While
increased teacher hiring brought the STR down from 47 to below 40, the effective STR
(ESTR), after accounting for teacher absences was still over 50 (having reduced from 64 in
2003 to 52 in 2010). The variation in teacher absence across states remains high. At one
end, several top performing states have teacher absence rates below 15%, while at the
other end, the poorest performing state, Jharkhand, has a teacher absence rate of 46%. Our
panel-data analysis, where we correlate changes in village-level teacher absence with
changes in teacher and school characteristics, and administrative and community-level
monitoring, yields two robust correlations. First, reductions in the school-level student-
teacher ratio (STR) are correlated with an increase in teacher absence, suggesting that
the potential benefits from investing in more teachers and lower STR may be partly offset
by an increase in teacher absence. Second, better top-down administrative monitoring is
strongly correlated with lower teacher absence. Absence rates were 6.5 percentage points
lower in villages with regular public school inspections relative to those without, which
is a 25% reduction in overall absence and a 40% decline in unauthorized absence.4 One way
to estimate the cost of teacher absence is to calculate the salary cost paid by the
government to teachers for days of work that they did not attend. We estimate this fiscal
cost to be over $1.5 billion per year, which is around 60% of the entire revenue collected
from the special education tax used to fund SSA in 2010.5 Teacher salaries typically
account for over 80% of non-capital education spending (Dongre et al., 2014), and the most
expensive component of the recently passed Right to Education (RtE) Act in India is a
commitment to reduce STR from 40:1 to 30:1, by hiring more teachers at an additional cost
of $5  billion/year. Using the most conservative panel-data estimates of the correlations
between increased monitoring and reduced teacher absence, we estimate that improving
school governance (by hiring more supervisory staff) could be over ten times more cost
effective at increasing effective student-teacher ratio (net of teacher absence) than
hiring more teachers. These calculations suggest that the marginal returns to investing in
an inefficiency-reduction strategy (through better monitoring and governance of the
education system) are likely to be much higher than a typical input-augmentation strategy.
This paper makes several contributions to the literature on public economics in low-income
countries. First, teacher absence is now widely used as a governance indicator in
education in low- and middle-income countries.6 We update estimates of teacher absence in
rural India from 2003 and show that despite substantial increases in education spending
over the last decade, improvements on this key measure of governance have been more
modest. While corruption in education spending has been shown to hurt learning outcomes
(Ferraz et al., 2012), our results highlight the importance of also focusing on governance
issues that lead to significant amounts of ‘passive’ waste and inefficiency on an ongoing
annual basis, but may not obtain as much media attention as one-off corruption scandals
(Bandiera et al., 2009; World Bank, 2010). Second, the fact that decreases in STRs are
correlated with increased teacher absence underscores the importance of distinguishing
between average and marginal rates of corruption and waste in public spending. Niehaus and
Sukhtankar (2013) propose this terminology in the context of wages paid in a public-works
program in India and find that marginal rates of leakage are much higher than average
rates. We find the same result in the context of teachers and show that the effective
absence rate of the marginal teacher hired is considerably higher than the average absence
(because of the increased absence among existing teachers). This result, from a large all-
India sample, mirrors smaller-sample experimental findings in multiple settings. Duflo et
al. (2015), and Muralidharan and Sundararaman (2013) present experimental evidence (from
Kenya and India) showing that provision of an extra teacher to schools led to an increase
in the absence rate of existing teachers in both settings. In other words, additional
spending on school inputs (of which teacher salaries are the largest component) was
correlated with increased inefficiency of spending. Third, improvements in top-down
administrative monitoring (inspections) are more strongly correlated with reduced teacher
absence than improvements in bottom-up community monitoring (PTA meetings), consistent
with experimental evidence on the relative effectiveness of administrative and community
audits on reducing corruption in road construction in Indonesia (Olken, 2007). More
broadly, a growing body of experimental evidence points to the effectiveness of audits and
monitoring (accompanied by rewards or sanctions) in improving the performance of public-
sector workers and service providers (including Olken (2007) in Indonesia; Duflo et al.
(2012) in India; and Zamboni and Litschig (2016) in Brazil). Our panel-data estimates
using data from an “as is” nationwide increase in monitoring of schools provide
complementary evidence to smaller-scale experiments and suggest that investing in better
governance and monitoring of service providers may be an important component of improving
state capacity for service delivery in low-income countries (Besley and Persson, 2009;
Muralidharan et al., 2016). Finally, recent research has pointed to ‘misallocation’ of
capital and labor in low-income countries as an important contributor to lower total
factor productivity (TFP) in these settings (Hsieh and Klenow, 2009), and has also
documented that a plausible reason for this misallocation is that ‘management quality’ is
poorer in low-income countries, and that public-sector firms are managed especially poorly
(Bloom and Van Reenen, 2010). Our results provide a striking example of weak management
and misallocation in publicly-produced primary education in India (a sector that accounts
for over 3% of GDP in spending). In particular, our estimates suggest that reallocating a
portion of the $5 billion/year increase in education spending budgeted for hiring more
teachers towards measures focused on reducing teacher absence (for instance, by hiring
more supervisory staff) may be a much more cost effective way of increasing effective
teacher-student contact time. Thus, misallocation is likely to be a first-order issue in
this setting, and reallocating education spending towards better governance may
substantially increase TFP in publicly-produced education.7 The rest of this paper is
organized as follows: Section 2 discusses our empirical methods and analytical framework.
Section 3 reports summary statistics on school inputs and teacher absence. Section 4
presents the cross-sectional and panel regression results. Section 5 discusses the fiscal
costs of weak governance and compares the returns to investing in better monitoring with
that from hiring more teachers. Section 6 discusses policy implications, and Section 7
concludes.

<h>DATA AND ANALYTIC FRAMEWORK</h>
---------------------------

The nationally-representative sample used for the 2003 surveys, which our current study
uses as a base, covered both urban and rural areas across the 19 most populous states of
India, except Delhi. This represented over 95% of the country's population. The 2010
sample covered only rural India. The sampling strategy in 2010 aimed to maintain
representativeness of the current landscape of schools in rural India, and to maximize the
size of the panel. We met these twin objectives by retaining the villages in the original
sample to the extent possible, while re-sampling schools from the full universe of schools
in these villages in 2010, and conducting the panel analysis at the village level.8
Enumerators first conducted school censuses in each village, from which we sampled up to
three schools per village for the absence surveys. During fieldwork, enumerators made
three separate visits to each sampled school over a period of 10 months from
January–October 2010.9 Data on school infrastructure and accessibility, finances, and
teacher demographics were collected once for each school (typically during the first
visit, but completed in later visits if necessary), while data on time-varying metrics
such as teacher and student attendance and dates of the most recent inspections and PTA
meetings were collected in each of the three visits. We also assessed student learning
with a test administered to a representative sample of fourth grade students in sampled
schools. See Appendix A and Tables A1 – A3 for further details on sampling and
construction of the village-level panel data set. Teacher absence was measured by direct
physical verification of teacher presence within the first fifteen minutes of a survey
visit. Data collected during the school census were used to pre-populate teacher rosters
for the sampled schools, so that enumerators could look for teachers and record their
attendance and activity immediately after their arrival at the school.10 Once teacher
attendance was recorded, all other data were collected using interviews of head teachers
and individual teachers.11 We record teachers as absent on a given visit if they were not
found anywhere in the school in the first fifteen minutes after enumerators reached a
school. We consider all the teachers in the school to be absent if the school was closed
during regular working hours on a school day, and respondents near the school did not know
why the school was closed or mentioned that the school was closed because no teacher had
arrived or they had all left early.12 To be conservative in our measure of absence, we
exclude all school closures due to bad weather, school construction/repairs, school
functions and alternative uses of school premises (for instance, elections). We also
exclude all part-time teachers, teachers who were transferred or reassigned elsewhere, or
teachers reportedly on a different shift. We construct a school infrastructure index by
adding binary indicators for the presence of drinking water, toilets, electricity, and a
library. We construct a remoteness index by taking the average of nine normalized
indicators of distance to various amenities including a paved road, bus station, train
station, public health facility, private health clinic, university, bank, post-office and
Ministry of Education office. A lower score on the remoteness index represents a better
connected school. During each survey visit, enumerators referred to written school records
to note the date of the most recent school inspection, and the date of the most recent
parent-teacher association (PTA) meeting. Average parental education of children in a
school is computed from the basic demographic data collected for the sample of fourth-
grade students chosen for assessments of learning outcomes. For most of the analysis in
this paper, we use the village as our unit of analysis and examine mean village-level
indicators of both inputs and outcomes because a large number of new schools had been
constructed between 2003 and 2010, including in villages that already had schools. This
school construction resulted from a policy designed to improve school access by ensuring
that every habitation with over 30 school-age children had a school within a distance of
one kilometer. Thus, to ensure that our sample was representative in 2010, and at the same
time amenable to panel data analysis relative to 2003, we constructed the panel at the
village level, with a new representative sample of schools drawn in the sampled
villages.13 All the results reported in this paper are population weighted and are thus
representative of the relevant geographic unit (i.e., state or all-India).

<hs>  Changes in inputs</hs>
  ~~~~~~~~~~~~~~~~~

The data show considerable improvements in school inputs between 2003 and 2010 along three
broad categories - teacher qualifications and working conditions, school facilities, and
monitoring (Table 1 - Panels A–C). The fraction of teachers with a college degree
increased from 41 to 58%, the fraction reporting that they were getting paid regularly
rose from 49 to 78%, and the fraction reporting the existence of teacher recognition
schemes rose from 50 to 81%. The fraction of teachers who report a formal teaching
credential fell from 77 to 68%, largely due to a significant increase in the hiring of
contract teachers (who are not required to have teaching credentials) in several large
states. In our data, the fraction of teachers on a temporary contract or ‘contract
teachers' increased from 6 to 30%. School facilities and infrastructure improved on almost
every measure. The fraction of schools with toilets and electricity more than doubled
(from 40% to 84% for toilets and 22% to 45% for electricity); the fraction of schools with
functioning mid-day meal programs nearly quadrupled (from 22% to 79%); the fraction of
schools with a library increased by over 35 %(from 51% to 69%), and almost all schools now
have access to drinking water (96%). Initiatives outside the education ministry to
increase road construction have also led to increased proximity of schools to paved roads
increasing the accessibility of schools for teachers who choose to live farther away.
Relative to the distribution observed in 2003, a summary index of school infrastructure
improved by 0.9 standard deviations.14 We also find improvements in both ‘top-down’
administrative and ‘bottom-up’ community monitoring of schools over this period. The
fraction of schools inspected in the three months prior to a survey visit increased from
38% to 56%. The extent of community oversight of schools, measured by the frequency of PTA
meetings also increased: The probability that a PTA meeting took place during the three
months prior to a survey visit increased from 30% to 45%. Overall, Table 1 (Panel A–C)
confirms that the Government of India's increased focus on primary education in the past
decade did lead to significant improvements in input-based measures of school quality, as
well as administrative and community monitoring.

<hs>  Changes in teacher absence</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~

We now turn to changes in teacher absence. Table 1 (Panel D) shows that the population-
weighted national average teacher absence rate for rural India fell from 26.3 percent% to
23.6%, a reduction of 10%. Since students receive reduced teacher attention when teachers
are absent, we divide the STR by “1 - teacher absence rate” to obtain the effective
student teacher ratio (ESTR). Although the all-India STR had been reduced to below 40 in
this period, the effective STR after accounting for teacher absence was still over 52. We
present state-level data on teacher absence rates and ESTR for 2003 and 2010 in Table
A4.15 Chaudhury et al. (2006) find a strong negative correlation between GDP/capita and
teacher absence rates (both across countries and within Indian states). Hence, one way to
interpret the magnitude of these changes is to compare them with the expected reduction in
teacher absence that may be attributed simply to the economic growth that has taken place
in this period. Using a growth accounting (as opposed to causal) framework, we can
decompose the change in teacher absence into a component explained by changes in
GDP/capita (as a proxy for ‘inputs') and one explained by a change in governance (a proxy
for TFP). Cross-sectional estimates from the 2003 data suggest that a 10 percent increase
in GDP/capita is associated with a 0.6 percentage point reduction in teacher absence.16 In
the period between 2002 and 2010, real GDP/capita in India had grown by 38%. Thus, growth
in GDP/capita over this period should have by itself contributed to a reduction in teacher
absence of 2.4%. Our estimate of the change in teacher absence rate is exactly in this
range, and suggests that the reduction of teacher absence we document is consistent with a
proportional increase in ‘inputs' into education, but a limited improvement in TFP in this
period. We discuss the policy implications of this result in the conclusion.

<hs>  Stated reasons for absence, teaching activity, and official records</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In cases where a teacher was not found in the school, enumerators asked the head teacher
(or senior-most teacher present) for the reason for absence. These stated reasons are
summarized in Table 2 (Panel A). Two categories of clearly unauthorized absence (school
closure during working hours and no valid reason for absence) account for just under half
the cases of teacher absence (48%), which provides a lower bound on the extent of
unauthorized absences of 11.3 percentage points. The two other categories of stated
absence (authorized leave and official duties) that account for 52% of the observed
absence are potentially legitimate but cannot be verified. While head teachers may
overstate the extent of official duties to shield absent colleagues, they should have no
reason to understate it. We can, therefore, reasonably treat the stated reasons for
absence as an upper bound for duty-induced absence. This yields the important finding that
one commonly cited reason for teacher absence - namely, that teachers are often asked to
perform non-teaching duties such as conducting censuses and monitoring elections - is a
very small contributor to the high rate of observed teacher absence. Table 2 - Panel A
shows that official non-teaching duties account for less than 1% of observations and under
4% of the cases of teacher absence (these results are unchanged from 2003). In cases where
the teacher was present, enumerators recorded the activity that the teacher was engaged in
at the point of observation: 53% of teachers on the payroll were found to be actively
teaching, and another 4% were coded as passively teaching (defined as minding the class
while students do their own work). Just over 19% of teachers were in school but were
either not in the classroom or not engaged in any teaching activity while in the classroom
(Table 2 - Panel B). Thus a total of 42% of teachers on the payroll were either absent or
not teaching at the time of direct observations.17 Finally, enumerators also recorded
whether a teacher had been marked as present in the log-books on the day of the visit and
also on the previous day, and we see in Table 2 - Panel C that going by these records
would suggest a much lower teacher absence rate of 16% using the same day's records, or as
low as 10.2% using the previous day's records (this was not collected in 2003).18 These
data highlight the importance of measuring teacher absence by direct physical verification
as opposed to official records on log books.

<hs>  Correlates of teacher absence in 2010</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Table 3 presents village-level cross-sectional regressions between indicators of school
quality and teacher absence in 2010. Column 1 shows the mean level of each covariate in
the sample, columns 2–4 present the coefficients on each indicator in individual
regressions with the dependent variable being teacher absence, while columns 5–7 do so in
multiple regressions that include all the variables shown in Table 1 as regressors. We
first show the regressions with no fixed effects, then with state fixed effects, and
finally with district fixed effects. The comparison of results with and without state
fixed effects is important for interpretation. Many indicators of school quality vary
considerably across states in a manner that is likely to be correlated with other measures
of governance and development as well as the history of education investments in these
states. On a similar note, while primary education policy is typically made at the state
level, there is often important variation across districts within a state based on
historical as well as geographical factors (Banerjee and Iyer, 2005; Iyer, 2010). Thus,
specifications with district fixed effects that are identified using only within-district
variation are least likely to be confounded by omitted variables correlated with
historical or geographical factors. However, there may still be important fixed omitted
variables across villages (such as the level of interest in education in the community)
that are correlated with both measured quality of schools and teachers as well as teacher
absence. We therefore present the cross-sectional regressions in Table 3 for completeness
and focus our discussion on the village-level panel regressions presented in Table 4.
Overall, there are few robust correlations across all specifications except that schools
that have been inspected recently have lower rates of absence. One important result in the
correlations is that there appears to be no significant relationship between teacher
salary and the probability of teacher absence. Since salary data were not collected in the
2003 survey, this variable is not included in the panel analysis below.

<hs>  Correlates of changes in teacher absence between 2003 and 2010</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Since Eq.(1) differences away fixed unobserved heterogeneity at the village level (and
therefore at the state and district level as well), the inclusion of state and district
fixed effects in the specification controls for average state and district specific
changes over time in both the left-hand and right-hand side variables. Thus our panel
results with state and district fixed effects are least likely to be confounded with time-
invariant and time-variant omitted variables.19 However, it is also worth noting that such
a specification biases us against detecting small effects. First, first-differencing
leaves us with less variation in the explanatory variables, which will increase standard
errors. Second, to the extent there is measurement error in the explanatory variables,
first differencing would also increase the attenuation bias. This is why we focus our
discussion and interpretation of the results on the ones that are robustly significant and
do not treat lack of evidence of significant effects as strong evidence in favor of null
effects. Nevertheless, the results in Table 4 suggest that several plausible narratives
for the reasons for teacher absence seen in the cross-sectional data reported in Kremer et
al. (2005) are not supported in the panel data regressions. In particular, unlike in
Kremer et al. (2005), we find no correlation between changes in school infrastructure or
proximity to a paved road and teacher absence. We also find no correlation between changes
in teacher professional qualifications or professional conditions (such as regularity of
pay) and changes in teacher absence.20 We find two robust relationships in the panel
regressions, where we define ‘robust’ as correlations that are significant in both
individual and multiple regressions; significant in all three main specifications (no
fixed effects, state fixed effects, and district fixed effects) and consistent across all
specifications (we cannot reject that the estimates are the same across specifications).
We discuss these two results below.

        Reductions in STR are correlated with increased teacher absence

        First, villages that saw a reduction in student-teacher ratio (STR) have
        significantly higher rates of teacher absence. A 10% reduction in STR is
        correlated with a 0.5% increase in average teacher absence, and these estimates
        remain stable when we include state and district fixed effects and are unchanged
        when we include a full set of controls (also measured in changes). Changes in STR
        reflect changes in enrollment as well as in the number of teachers, and a higher
        STR may affect teacher absence through both enrollment and number of teachers.
        First, having more students enrolled may increase the cost to teachers of being
        absent since there are more students (and parents) who may complain. Second, the
        most common outcome for students when their teacher is absent is that they are
        combined with other classes/grades whose teachers are present.21 Thus, having more
        teachers in the school may make it easier for teachers to be absent (since other
        teachers can handle their class).22 These correlations should not be interpreted
        as causal (for instance, student enrolment may decline in response to increased
        teacher absence), but they are consistent with a causal relationship between
        increased teacher hiring and increased absence of existing teachers that has been
        established experimentally in India (Muralidharan and Sundararaman, 2013) and
        other low-income countries such as Kenya (Duflo et al., 2015). Our results provide
        complementary evidence and greater external validity to these experimental
        results, and suggest that the benefits of additional teacher hiring to reduce STR
        may be attenuated by increased teacher absence (in contexts with weak governance
        of education systems).

        Increasing monitoring is correlated with reduced teacher absence

        The second robust result in the panel data estimates is the strong negative
        correlation between improved school monitoring and teacher absence. In each of the
        three visits to a school, enumerators recorded the date of the most recent
        inspection, and we average across the three visits across all the sampled schools
        in the village to construct the variable “Probability of being inspected in last 3
        months”, which ranges from zero (none of the schools in the village were inspected
        in the prior three months in any of the three visits) to one (all the schools in
        the village were inspected in the prior three months in all of the three visits).
        We find that villages where the probability of inspection in the past three months
        increased from zero to one had a reduction in average teacher absence of between
        6.4 and 8.2 percentage points (a 27–35 percent reduction in teacher absence).23
        While these results are based on correlations, we present several pieces of
        evidence consistent with a causal effect of increased school inspections on
        reduced teacher absence. First, we look at the categories of stated reasons for
        absence (official duty, authorized leave, and unauthorized absence), and find that
        increases in inspection probability are correlated only with reductions in
        unauthorized teacher absence, but not with reductions in teacher absence due to
        either official duty or authorized leave (Table 5). Second, we examine the extent
        to which changes in inspection frequency can be explained by other observable
        factors, and find that there are no correlations between changes in inspection
        frequency and changes in other observable measures of school quality that are
        significant across our three standard specifications (Table A5). Third, we use the
        technique developed by Altonji et al. (2005) to show that the ratio of
        unobservable to observable correlates of changes in teacher absence would have to
        be over a factor of 10 for these results to be completely explained by omitted
        variables (Table A6). Given the very rich data we have on observable changes in
        school quality, and the fact that our estimates are unchanged even after including
        state and district fixed effects, this is unlikely to be the case.24 Finally,
        these results are also consistent with experimental evidence from India that finds
        significant reduction in teacher absence in response to improved monitoring and
        rewards linked to better teacher attendance (Duflo et al., 2012). This
        experimental study, however, was carried out in a small sample of informal schools
        in one district in India. Thus, our estimates using nationally-representative
        panel data of rural public schools across 190 districts provide complementary
        evidence that improved ‘top down’ administrative monitoring may have a substantial
        impact on reducing unauthorized teacher absence. In contrast, there is less
        evidence that increases in ‘bottom up’ monitoring by the community (measured by
        whether the PTA had met in the past 3  months) are correlated with reductions in
        teacher absence (Table 4). This is consistent with the experimental results
        reported in Olken (2007) on the impacts of monitoring corruption in Indonesia.
        These results should not be interpreted as suggesting that bottom-up monitoring
        cannot be effective, since it is also likely that they reflect differences in the
        effective authority over teachers possessed by administrative superiors (high)
        versus parents (low). PTAs in India typically do not have authority to appoint or
        retain regular civil-service teachers, and they cannot sanction teachers for
        absence or non-performance (Banerjee et al., 2010). Inspectors and administrative
        superiors, on the other hand, possess considerable authority over teachers. Their
        powers include the ability to demand explanations for absence, to issue verbal or
        written warnings, to make adverse entries in teachers' performance records, to
        recommend against a pay increment, to suspend a teacher, and in extreme cases to
        initiate proceedings to fire a teacher (see Ministry of Education (1964-1966) for
        a detailed discussion of the design of the Indian school inspection system and the
        powers it provides inspectors). While it is rare for teachers in India to actually
        get fired for absence (Kremer et al., 2005), and also true that politically-
        connected teachers can evade sanctions for absence (De and Dreze, 1999; Kingdon et
        al., 2014), the teacher service rules include several provisions that make it
        possible for inspectors to significantly raise the costs of teacher absence and
        thereby reduce it. A striking recent example of how a motivated school inspector
        in India was able to reduce teacher absence is provided by Anand (Feb. 19,
        2016).25 In interpreting the result on school inspections, it is useful to
        consider why there might be variation in the frequency of inspections across
        villages and what this would imply for a causal interpretation. One obvious
        explanation is that inspectors are more likely to visit more accessible villages,
        but the data do not support this hypothesis since there is no correlation between
        changes in the remoteness index and changes in inspection rates (Table A5).
        District-level interviews on school governance in India suggest two important
        reasons for the variation in inspection frequency. The first is staffing.
        Districts are broken down further into administrative blocks, and schools within
        blocks are organized into clusters. School supervision is typically conducted by
        “block education officers” and “cluster resource coordinators”. We find that a
        significant fraction of these posts are often unfilled. For instance, in 19% of
        the cases (where we have data) even the position of the “District Education
        Officer (DEO)”, the senior-most education official in a district, was vacant
        (Centre for Policy Research, 2012).26 Further, there is high turnover in the
        education administration (the average DEO had a tenure in office of just one year)
        creating periods when the positions are vacant during transitions. The lack of
        supervisory staff at the block-level is even more acute, as 32% of these positions
        were estimated to be vacant in 2010 (the year of our survey) even by an official
        government report (13th JRM Monitoring Report, 2011). Our interviews suggest that
        these staffing gaps at the block and cluster level are the most important source
        of variation in inspection frequency within districts, since blocks and clusters
        without supervisory staff are much less likely to get inspected. The second source
        of variation in inspections is the diligence of the concerned supervisory officer.
        Even if all the positions of supervisory staff were filled, there would be
        variation in the zealousness with which these officers visited villages/schools,
        which might lead to some areas being inspected more often than others based on
        whether they were in the coverage area of a more diligent officer or not. However,
        since supervisors are typically assigned a coverage area of clusters or blocks
        that comprise many villages, variation in monitoring frequency that is driven by
        supervisor-level unobservable characteristics is unlikely to be correlated with
        other village-level characteristics that are also correlated with absence. Of
        course, this source of variation has implications for thinking about the likely
        effectiveness of hiring new supervisory staff (some of whom may be less diligent).
        We discuss these in Section 5.3.

<hs>  Teacher absence and student learning outcomes</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

While not very precise, the estimates in Table 6 (column 5) suggest that both reductions
in log(STR), and reductions in log(1-Absence) matter equally for improved test scores.
Column 6 of Table 5 shows that once log(ESTR) is controlled for there is no independent
effect of teacher absence on learning outcomes, suggesting that the main mechanism by
which teacher absence affects learning outcomes is through increasing the ESTR. The
stronger relationship between teacher absence and student learning outcomes seen in
columns 2 and 3 (that do not include state or district fixed effects) suggests that
teacher absence is likely correlated with other measures of education governance at the
state and district levels, and highlights why our preferred specifications are the ones
with district fixed effects. Our data, which are collected seven years apart and have only
mean village-level test scores, are not ideal for studying the impact of teacher absence
or other school characteristics on test scores (the ideal specifications would use annual
panel data on student test scores matched to these characteristics and estimate value-
added models of student learning). But it allows us to present suggestive evidence on the
negative correlations between teacher absence and student learning outcomes that are
consistent with other studies using better data that find similar results.28 The results
in Table 6 also help illustrate that teacher absence can attenuate the benefits of
reducing STR, and that reducing effective STR can be done both by reducing STR and by
reducing teacher absence. We consider the relative cost effectiveness of these approaches
in the next section.

<hs>  The fiscal cost of teacher absence</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

High levels of teacher absence translate into considerable waste of public funds since
teacher salaries are the largest component of education spending in most countries,
including India. One way of estimating these costs is to calculate the total salary cost
paid to teachers for days of work that they were expected to attend, but do not. Note that
this is not a cost that would be saved if teacher absence were to be reduced (since the
full teacher salaries would be paid in either case). However, it is standard in the
corruption literature to measure the cost of corruption by the amount of public
expenditure that does not reach its intended goal (often referred to as ‘leakage’), and to
measure the impact of interventions to reduce corruption by quantifying the reduction in
leakage, even if there is no reduction in fiscal outlay (Reinikka and Svensson,
2004;Reinikka and Svensson, 2005;Niehaus and Sukhtankar, 2013;Muralidharan et al.,
2016).29 We follow a similar approach here by first quantifying the salary cost of absence
as an estimate of ‘leakage’ in education spending, and then using these costs as the
metric to evaluate alternate policy approaches to reducing ESTR. Calculating the cost of
teacher absence requires us to estimate and exclude the extent of legitimate absence from
our calculations. As part of the institutional background work for this project, we
obtained teacher policy documents from several states across India. Analysis of these
documents indicates that the annual allowance for personal and sick leave is 5% on average
across states. This is close to the survey estimate of 5.9%(Table 2), but we use the
official data since the stated reasons may be over-reported. Estimating the extent of
legitimate absence due to ‘official duty’ (outside the school) is more difficult because
there are no standard figures for the ‘expected’ level of teacher absence for official
duties. Policy norms prescribe minimal disruption to teachers during the school day and
stipulate that meetings and trainings be carried out on non-school days or outside school
hours. Since we are not able to verify the claim that teachers were on official duty, and
there is evidence that head teachers try to cover up for teacher absences by claiming that
these are due to ‘official duties', our default estimate treats half of these cases as
legitimate. This gives us a base case of legitimate absence of 8%(5% authorized leave, and
3% official duty). We also consider a more conservative case where the legitimate rate of
absence is 10%. This 8–10% range of legitimate absence also makes sense because the
fraction of teacher observations that are classified as either ‘authorized leave’ or
‘official duty’ is in this range for the five states with the lowest overall absence rates
- even treating the stated reasons for absence as being fully true (tables available on
request). To estimate the cost of teacher absence, we use teacher salary data from our
surveys and use administrative (DISE) data on the number of primary school teachers by
state.30 We provide three estimates of the fiscal cost of teacher absence based on
assuming the rate of legitimate teacher absence to be 8, 9, and 10 percent% respectively,
and these calculations suggest that the annual fiscal cost of teacher absence is around
Rs.81 –93 billion, which is around US$1.4–1.6 billion/year at 2010 exchange rates (Table 7
- Panel A).

<hs>  Calculating the returns to better governance in education</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Using the results in Table 4, we calculate the returns to a marginal increase in the
probability of a school being inspected. We make the following assumptions: (a) enough
supervisory staff are hired to increase the probability of a school being inspected in the
past 3  months by 10 percentage points (relative to a current probability of 56%); (b)
increasing inspection probability by 10 percentage points would reduce mean teacher
absence across the schools in a village by 0.64 percentage points (the most conservative
estimate of the correlation between increased inspection probability and reduced teacher
absence from Table 4); (c) the full cost (salary and travel) of a supervisor is 2.8 times
that of a teacher; (d) a supervisor works 200  days per year and can cover 2 schools per
day.31 The results of this estimation are presented in Table 7 (Panel B) and we see that
the cost of hiring enough supervisors to increase the probability of a school being
inspected by 10 percentage points is Rs.448  million/year (see Table A8 for state-level
calculations). However, the reduction in wasted salary from this investment in terms of
reduced teacher absence amounts to Rs.4.5  billion/year, suggesting that investing in
better monitoring would lead to a reduction in ‘leakage’ of teacher salaries (defined as
salary payments for days when teachers do not attend work) that is around ten times
greater than the cost of increasing monitoring by hiring more supervisory staff.

<hs>  Input augmentation versus inefficiency reduction</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

To compare the relative cost effectiveness of hiring more teachers (input augmentation)
versus hiring more supervisors to reduce teacher absence (inefficiency reduction) as a way
of reducing the ESTR, we calculate the salary cost of hiring more teachers to achieve the
same reduction in ESTR that we estimate would be obtained by increasing the inspection
probability by 10 percentage points. We estimate this to be Rs. 5.7  billion/year (Table 7
- Panel B; Table A8 provides detailed state-level calculations), and see that increasing
the probability of inspection would be 12.8 times more cost effective at reducing ESTR
than doing so by hiring more teachers (on the current margin).32 The difference in the
relative cost effectiveness of the two policy options is large enough that hiring more
supervisors rather than teachers is likely to be a more cost effective way of reducing
ESTR (on the current margin) even if the supervisors were to work less efficiently than
assumed in these calculations. For instance, if supervisors were absent at the same rate
as teachers (say 25 %), allocating marginal funds to hire an additional supervisor would
still be nearly ten times more cost effective at reducing ESTR than using those funds to
hire an additional teacher.33

<h>POLICY IMPLICATIONS</h>
-------------------

The main caveat to using our results to recommend a universal policy of hiring more
supervisors to scale up the frequency of school inspections is that our estimates are
based on correlations and may not be convincing enough to warrant a universal scale up.
Nevertheless, it is worth noting that both our key results - the correlation between
increased monitoring and reduced teacher absence, and the correlation between lower STR
and increased teacher absence - are consistent with experimental evidence from smaller-
scale, which increases our confidence in their validity. Further, our estimates are based
on an expansion of existing system of inspections, and use nationwide panel data (which
mitigates omitted variables concerns) representing close to a billion people, and
complement results from smaller-scale randomized experiments warranting them greater
external validity for several reasons. First, while our results support results from
smaller randomized experiments, there is evidence that experimentally-estimated positive
results of interventions that are implemented by NGOs may not be replicated when the
programs are implemented by governments (Banerjee et al., 2008). Second, there is also
evidence of site-selection bias where implementing partners are more likely to be willing
to rigorously evaluate programs in locations where they are more likely to be successful
(Allcott, 2015). Finally, even in the absence of such a bias, most experiments are
conducted in very few sites, and may yield imprecise treatment effects (for inference over
a larger population) in a setting where unobserved site-specific covariates may interact
with the treatment (Pritchett and Sandefur, 2013).34 Thus, even if small-scale experiments
are unbiased within sample, they may be biased and also imprecise for population-level
inference. In other words, there is likely to be a trade-off between the potential omitted
variable bias in our panel-data estimates on one hand, and the advantages of greater
precision, “as is” implementation, and unbiased site selection on the other. We do not
attempt to quantify this trade-off in this paper since we have no objective basis of doing
so. However, one way of reconciling this trade-off is to conduct a substantial nationwide
expansion of school inspections by hiring more staff in the context of a large
experimental evaluation. From a decision-theoretic perspective, our results are strong
enough to support such a policy even if there is only a 1% chance that our estimates are
causal. In Appendix B, we formally show that, barring extreme priors, a policy-maker
interested in lowering effective student-teacher ratio will find it cost-effective to
invest in or scale-up monitoring of teachers.

<h>CONCLUSIONS</h>
-----------

The central and state governments in India have considerably increased spending on primary
education over the past decade. We contribute towards understanding the impact of these
substantial nationwide investments in primary education in India by constructing a unique
nationally-representative panel data set on education quality in rural India. We find that
there has been a substantial improvement in several measures of school quality including
infrastructure, student-teacher ratios, and monitoring. However, teacher absence rates
continue to be high, with 23.6% of teachers in public schools across rural India being
absent during unannounced visits to schools. Using village-level panel data, we find two
robust correlations in the panel data that provide external validity in nationally-
representative data to results established in smaller-scale experiments. First, reductions
in student-teacher ratios are strongly correlated with increased teacher absence,
suggesting that increased spending on hiring additional teachers was accompanied by
increased inefficiency, which may limit the extent to which additional spending may
improve outcomes. Second, increases in the frequency of inspections are strongly
correlated with lower teacher absence, suggesting that of all the investments in improving
school quality, the one that was most effective in reducing teacher absence was improved
administrative monitoring of schools and teachers. We calculate that the fiscal cost of
teacher absence is over $1.5 billion per year, and estimate that investing in improved
governance by increasing the frequency of monitoring would be over ten times more cost
effective at increasing student-teacher contact time than doing so by hiring additional
teachers. In interpreting our results, it may be useful to think of the performance of the
education system (measured by the level of teacher absence) as comprising two components -
‘inputs' into the production of education that expand with income growth (such as school
infrastructure, class size, and teacher salaries), and the efficiency of the use of these
inputs (which would correspond to the TFP of education production). Our results show that
the Indian education system has made significant progress on the former, but made less
progress on the latter. They also suggest that pivoting public expenditure away from
simply augmenting inputs towards policies that increase the efficiency of inputs may
considerably increase the productivity of education spending, and thereby enable
achievement of improved human capital outcomes at any given level of per-capita income.
One promising way of reducing inefficiency is improving school governance and achieving
such a reallocation of resources would be to expand the existing system of administrative
monitoring of teachers and schools by hiring more supervisory staff. Our calculations
indicate that such a marginal expansion could (on the current margin) have a significant
impact on reducing teacher absence, and that this would be highly cost effective in terms
of reducing the fiscal cost of weak governance. More broadly, our results suggest that the
returns to investing in state capacity to better monitor the implementation of social
programs in low-income countries may be quite high, and that at the very least there is a
strong case for expanding such programs in the context of large experimental evaluations
of “as is” implementation to obtain more precise estimates of their benefits.35


<h>REFERENCES</h>
----------

  [2] Hunt Allcott. Site selection bias in program evaluation. doi:10.1093/qje/qjv015
  [3] Joseph G. Altonji, Todd E. Elder, Christopher R. Taber. Selection on observed and unobserved variables: Assessing the effectiveness of Catholic schools. doi:10.1086/426036
  [5] Oriana Bandiera, Andrea Prat, Tommaso Valletti. Active and passive waste in government spending: Evidence from a policy experiment. doi:10.1257/aer.99.4.1278
  [6] Abhijit V. Banerjee, Rukmini Banerji, Esther Duflo, Rachel Glennerster, Stuti Khemani. Pitfalls of participatory programs: Evidence from a randomized evaluation in education in India. doi:10.1257/pol.2.1.1
  [7] Abhijit V. Banerjee, Esther Duflo, Rachel Glennerster. Putting a band-aid on a corpse: Incentives for nurses in the Indian public health care system. doi:10.1162/JEEA.2008.6.2-3.487
  [8] Abhijit Banerjee, Lakshmi Iyer. History, institutions, and economic performance: The legacy of colonial land tenure systems in India. doi:10.1257/0002828054825574
  [9] Timothy Besley, Torsten Persson. The origins of state capacity: Property rights, taxation, and politics. doi:10.1257/aer.99.4.1218
  [10] Nicholas Bloom, John Van Reenen. Why do management practices differ across firms and countries?. doi:10.1257/jep.24.1.203
  [12] Nazmul Chaudhury, Jeffrey Hammer, Michael Kremer, Karthik Muralidharan, F. Halsey Rogers. Missing in action: Teacher and health worker absence in developing countries. doi:10.1257/089533006776526058
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<ART>The geometry of distributional preferences and a non-parametric identification approach: The Equality Equivalence Test
================================================================================

Authors: Rudolf Kerschbamer
DOI: 10.1016/j.euroecorev.2015.01.008
Year: 2015  |  Pages: 85-103
ASJC codes: 2002, 2003
Keywords: B41, C81, C90, D63, D64, Distributional preferences, Equality equivalence test, Other-regarding preferences, Social preferences, Social value orientations

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper proposes a geometric delineation of distributional preference types and a non-parametric approach for their identification in a two-person context. It starts with a small set of assumptions on preferences and shows that this set (i) naturally results in a taxonomy of distributional archetypes that nests all empirically relevant types considered in previous work; and (ii) gives rise to a clean experimental identification procedure - the Equality Equivalence Test - that discriminates between archetypes according to core features of preferences rather than properties of specific modeling variants. As a by-product the test yields a two-dimensional index of preference intensity.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Many economists׳ default assumption is that all agents are exclusively motivated by their
own material self-interest. This assumption is in sharp contrast to both day-to-day
experience and empirical evidence gathered by psychologists and experimental economists in
the last decades. This has aroused renewed interest in theories of other-regarding
preferences, where arguments beyond material self-interest enter the decision maker׳s
utility function.1 Typical examples of such arguments are other people׳s (material) well-
being (as in distributional preferences models),2 others׳ opportunities and expected or
observed behavior (as in reciprocity models),3 others׳ payoff expectations (as in guilt
aversion models),4 or others׳ other-regarding concerns (as in type based models).5 The
present paper focuses on the first of the above mentioned subclasses, i.e. on
distributional (or “social”) preferences, where besides one׳s own material payoff the
(material) well-being of others enters an agent׳s utility function. Distributional
preferences have been shown to be behaviorally relevant in important market and non-market
environments – see Sobel (2005) and Fehr and Schmidt (2006) for excellent surveys. The
current paper adds to this literature by proposing (i) a simple classification of
distributional preference types that nests almost all major classifications of archetypes
discussed in the economic and the social psychology literature; and (ii) a simple
identification procedure based on the classification. Identification of distributional
preferences has been the topic of numerous papers, of course – see Kerschbamer (2013) for
a thorough review of the literature. These pioneering studies – which have greatly
advanced our understanding of non-selfish behavior – suffer from at least one of two
methodological shortcomings. First, the tests employed typically discriminate between the
members of a somewhat arbitrary list of distributional types; and secondly, the
identification procedures typically rely on strong structural assumptions.6 Regarding the
former dimension – the set of distributional types tested for – previous studies either
start with a given list of types, or they employ a test design that allows discriminating
only between the members of a limited set of types.7 For instance, the path-breaking
dictator-game study by Andreoni and Miller (2002) distinguishes between selfish, Leontief
and perfect substitutes preferences, plus weak incarnations of those types; the follow-up
study by Fisman et al. (2007) employs a richer design and discriminates between self-
interested, lexself (lexicographic for self over other), social welfare and competitive
types plus some mixes thereof; the pioneering discrete choice study by Engelmann and
Strobel (2004) tries to disentangle efficiency concerns (defined as surplus maximization),
maximin preferences and (two modeling variants of) inequality aversion; Blanco et al.
(2011) discriminate between selfish and various intensities of piecewise linear inequality
aversion; Charness and Rabin (2002), Cabrales et al. (2010) and Iriberri and Rey-Biel
(2013) allow for self-interested, social welfare, difference-averse and competitive
preferences; and the ring-test – originally developed by social psychologists to assess
“social value orientations”8 and recently used by economists to identify type and
intensity of distributional concerns9 – discriminates between altruists, cooperators,
individualists, competititors, aggressors, martyrs, masochists and sadomasochists. Turning
to the second dimension – the structural assumptions imposed – the identification
procedures employed in previous studies typically rely on strong assumptions regarding the
form of the utility or motivational function meant to represent preferences. For instance,
the ring-test is based on the assumption of linear preferences; the studies by Cabrales et
al. (2010), Blanco et al. (2011) and Iriberri and Rey-Biel (2013) employ identification
procedures based on the piecewise linear model originally introduced by Fehr and Schmidt
(1999) as a description of self-centered inequality aversion and later extended by
Charness and Rabin (2002) to allow for other forms of distributional concerns and thereby
assume piecewise linearity; and Andreoni and Miller (2002), Fisman et al. (2007) and Cox
and Sadiraj (2012) check consistency with – and estimate parameters of – standard or
modified constant elasticity of substitution (CES) utility functions. Summing up the above
discussion we conclude (i) that there is neither an agreement in the literature on what
the relevant set of distributional basic motivations – defined as the manner in which
people care about the (material) well-being of others – is, nor on how to delimitate
distributional types; and (ii) that existing studies employ identification procedures that
rely on strong structural assumptions as, for instance, linearity, piecewise linearity or
standard or modified CES forms. By using a systematic approach based on a small set of
primitive assumptions on preferences, the present paper offers an improvement in both
dimensions. It shows (i) that this set of assumptions naturally results in a well
delineated, mutually exclusive and comprehensive distinction between nine archetypes of
distributional concerns; and (ii) that this set gives rise to a simple non-parametric
experimental test – the Equality Equivalence Test (EET) – that discriminates between the
archetypes according to core features of preferences rather than properties of specific
modeling variants or functional forms. As a byproduct the test yields a two-dimensional
index of preference intensity. While the primary purpose of this paper is methodological,
the experimental results obtained in an implementation of the EET also produce some
substantive insights. For instance, the result that – consistent with the theoretically
appealing assumption that distributional preferences are convex – about 95% of the
subjects reveal (weakly) more benevolent (less malevolent) preferences in the domain of
advantageous than in the domain of disadvantageous inequality. A second interesting detail
is that beyond selfish subjects, the empirically most frequent distributional archetypes
are those who exhibit (at least weakly) positive attitudes towards others in both domains
(i.e., altruism and maximin), while archetypes that imply a negative attitude in at least
one of the domains are by far less important empirically (the behavior of less than a
fourth of the subjects is consistent with any form of inequality aversion, for instance,
and the choices of less than 7% of the subject population are consistent with spite).10
The rest of the paper is organized as follows: Section 2 presents the assumptions on which
the analysis is based and argues that those assumptions are fulfilled by all major
modeling variants of distributional preferences discussed in the economic and the social
psychology literature. Section 3 introduces the proposed classification of preference
types based on the rate an agent is willing to trade between own monetary payoff and the
monetary payoff of another. Section 4 presents the proposed identification procedure – the
“Equality Equivalence Test” (EET). It starts (in Section 4.1) by conveying the intuition
behind the proposed identification approach and explaining its similarity to the Certainty
Equivalence Test. Section 4.2 presents the symmetric basic version of the test, and
Section 4.3 discusses several extensions. In Section 4.4 a two-dimensional index for
identifying the archetype and characterizing the intensity of distributional concerns –
the (x, y)-score – is introduced, and a graphical representation of the type–intensity
distribution is proposed. Section 4.5 relates the (x, y)-score to other measures of type
and intensity of distributional concerns. Section 5 illustrates the working of the EET by
reporting experimental results generated with the symmetric basic version of the test, and
Section 6 concludes. Implementation issues for the case where the test is used as a tool
in experimental economics (to address research questions in which distributional
preferences are expected to shape behavior, to control for subject pool effects, or to
help to interpret data from other unrelated experiments) are discussed in Appendix A.
Appendix B contains the instructions of the experiment reported in Section 5.

<h>ASSUMPTIONS</h>
-----------

Let a=(m, o) denote an income allocation that gives material payoff m (for “my”) to the
decision maker (DM or “agent”) and material payoff o (for “other”) to the other person.
The space of feasible income allocations is assumed to be the non-negative orthant of R2
and is denoted by A. Throughout we assume that the DM is equipped with a preference
relation over income allocations, which we denote by ≽. Technically, ≽ is a binary
relation on A, allowing the DM to compare pairs of allocations a, a*∈A. We read a≽a* as
“the DM weakly prefers allocation a to allocation a*” and denote the asymmetric and the
symmetric part of ≽ by ≻ and ~, respectively.11 For the DM’s preferences we require:
(completeness, transitivity and continuity): The DM’s preference relation on income
allocations is complete, transitive and continuous. That is, for ≽ it holds that: for
every pair a, a′∈A, either a≽a′, or a′≽a (or both); for every triple a, a′, a*∈A, if a≽a′
and a′≽a*, then a≽a*; for every two sequences a1, a2, a3,… and a′1, a′2, a′3,… in A, if
the sequence a1, a2, a3,… converges to a and the sequence a′1, a′2, a′3,… converges to a′,
and if ai≽a′i for each i, then a≽a′. Completeness (i.e., the first part of Assumption 1)
requires that the DM can compare any two income allocations; transitivity (the second
part) adds the requirement that the preferences of the DM are internally consistent; and
continuity (the last part) says that the DM′s preferences do not exhibit “jumps”, with,
for example, the DM preferring each element in the sequence a1, a2, a3,… to a′, but
suddenly reversing her preferences at the limiting point of the sequence. While ordering
(completeness and transitivity) is important for the arguments below (as it is for
substantial parts of economic theory), continuity is not.12 As shown by Eilenberg (1941)
the three parts of Assumption 1 together imply that the DM′s preferences can be summarized
by means of a continuous utility or motivational function u(m, o) that assigns a real-
valued index to every (m, o)∈A. (strict m-monotonicity): The DM′s preference relation on
income allocations is strictly monotonic in the own material payoff. That is, comparing
any two income allocations (m, o) and (m′, o) in A with the same level of o, (m, o)≻(m′,
o)⇔m>m′ and (m, o)~(m′, o)⇔m=m′. Strict m-monotonicity requires that – holding the
material payoff of the other person constant – the DM strictly prefers more own material
payoff to less own material payoff. This is quite a natural assumption. It is violated,
for instance, if the DM is willing to burn her own monetary payoff because she feels bad
whenever she has (much) more than the other person. Such behavior is essentially never
observed in experiments. In terms of utility representation, Assumption 2 translates to
the requirement that for every (m, o)∈A and ∆∈R++ we have u(m+∆, o)>u(m, o). (piecewise
o-monotonicity): The DM′s preference relation between two income allocations that have the
same own material payoff for the DM but different payoffs for the other person depends
only on whether the DM is ahead or behind. That is, comparing any two income allocations
(m, o) and (m, o′) in A with the same level of m and o<o′, the DM′s preference
relationship between (m, o) and (m, o′) (i.e., whether ≻, ≺, or ~ holds) is constant for
all o, o′, m such that o>m and is also constant for all o, o′ m such that m>o′ (but
potentially different between the two domains). Piecewise o-monotonicity requires that the
DM′s general attitude towards the other person (i.e., whether she is benevolent, neutral,
or malevolent to the other) depends only on whether the other person has more or less
monetary payoff than the DM herself. In terms of utility representation, it translates to
the requirement that for every ∆∈R++ the sign of the difference u(m, o+∆)−u(m, o) is
constant for all (m, o)∈A with o>m and is also constant for all (m, o)∈A with o+∆<m (but
potentially different between the two domains). Piecewise o-monotonicity is both
permissive and restrictive, depending on the perspective. It is permissive because it
allows for all major variants of distributional preferences that have been discussed in
the economic literature – see the discussion at the end of this and in the next section.
Piecewise o-monotonicity is also restrictive because it implies (i) that preferences only
depend on monetary outcomes, not on the way they are achieved (this is the defining
feature of distributional preferences); and (ii) that the reference point for the
evaluation of allocations (if one is used) is an equal-material-payoffs allocation. Ad
(i): The implication that preferences only depend on monetary outcomes is likely to be
violated in many important applications. For instance, in strategic interactions (where
the other person has an opportunity to move and thereby a possibility to influence the
payoff of the DM) beliefs about intentions behind observed or expected action choices of
the other person potentially play a role (see the literature on reciprocity and related
concepts cited in Footnote 2). Also, in some games beliefs about the payoff expectations
of the other person seem to influence behavior (see the literature on guilt aversion and
related concepts cited in Footnote 3). Furthermore, in a richer environment, where agents
have more information on each other, beliefs about the other-regarding concerns of the
other person may play a role (as in the literature on type-based models cited in Footnote
4). Finally, features of the situation (such as context, entitlements, properties of the
outcome generating process, etc.) or the DM (such as a code of conduct, or a preference
for honesty) might shape behavior. Knowing that all those factors might be behaviorally
relevant in a richer environment, it seems important that distributional preferences are
identified in a non-strategic setting and a neutral frame to avoid confounds. This is not
to say that distributional preferences are unimportant in richer environments, of course,
but rather that they cannot be unambiguously identified there. Ad (ii): Some
distributional archetypes discussed in real life and in the literature (most importantly,
inequality aversion and egalitarian motives; maximin, Rawlsian and Leontief preferences;
and envy) are inevitably defined in terms of a “reference location”, where the DM׳s
general attitude towards the other changes from preferring higher payoffs for the other to
preferring lower payoffs. In theory, this reference location can be anything (an interval,
a point, or whatsoever), and it can differ among individuals. In existing models of
reference-dependent distributional concerns, the reference location is a point, and the
point is the egalitarian one for all individuals (see, for instance, Bolton, 1991; Mui,
1995; Fehr and Schmidt, 1999; Bolton and Ockenfels, 2000; or Charness and Rabin, 2002).
While Assumption 3 is more agnostic than existing models of reference-dependent
distributional concerns, it is still restrictive.13 For instance, there might exist
individuals who consider it fair to get 20% more than others but unfair to get 30% more.
Assumption 3 does not allow for this. While it would be feasible, in principle, to
generalize Assumption 3 (and the test relying on it) so as to allow for heterogeneous
reference points, this would seriously impair simplicity and transparency: Ultimately the
aim of the paper is to propose a classification of subjects in distributional preference
types that is helpful in organizing experimental data. For that purpose we need some kind
of clustering and not a different distributional type for each single individual. Stated
differently, as any model the approach proposed here is by design an abstraction of
reality, and hence is deliberately constructed so as to not explain some behavior, in
return for parsimony. While parsimony calls for a unique reference point, it does not
suggest equality as the reference point. Equality is suggested by normative considerations
and by empirical evidence. The normative basis of equality as a reference point is
discussed in some detail in Konow (1993) and in the working paper version of this article
(Kerschbamer, 2013). Regarding empirical evidence Andreoni and Bernheim (2009, p. 1607f)
cite several studies showing that equal sharing is common in the context of joint ventures
among business firms, partnerships among professionals, share tenancy in agriculture, and
bequests to children. They also provide evidence indicating that equality is a frequent
outcome of negotiation and conventional arbitration in the field. In lab-experiments the
assumption that the egalitarian outcome is somehow focal among subjects who change their
general attitude towards others at some point seems even more natural than in the field:
Subjects enter the laboratory as equals, their roles are assigned randomly and they have
absolutely no information about each other. It seems therefore quite plausible that those
subjects who attribute special meaning to an allocation (again, nothing in Assumption 3
requires them to do so) do this to the egalitarian one. And there is indeed considerable
support for this assumption in existing experimental data. For instance, one of the
stylized facts in standard dictator games is precisely that a sizeable fraction of the
subject population voluntarily cedes exactly half of the pie to the recipient, and that
very few subjects cede more (Camerer, 1997). This result survives even in experiments
where the action space is continuous and where the price for giving is quite high (see
Andreoni and Miller, 2002, for instance). The frequency of equal divisions is even higher
in ultimatum games, where expectations about the “reference point” of the recipient enter
the picture (see Camerer, 2003). While all this evidence indicates that the egalitarian
outcome has something special for a substantial fraction of subjects, it does not tell us
anything about the exact fraction of subjects for whom this is the case.14 But this is
exactly (one of) the question(s) the proposed test aims to address. (strict equal-
material-payoff-monotonicity): The DM′s preference relation on income allocations is
strictly monotonic in both payoffs along the ray m=o. That is, comparing any two income
allocations (m, o) and (m′, o′) in A with m=o and m′=o′, (m, o)≻(m′, o′)⇔m>m′ and (m,
o)~(m′, o′)⇔m=m′. Strict equal-material-payoff-monotonicity requires that more preferred
allocations are reached when the payoffs of both agents are increased along the 45° line.
In terms of utility representation it translates to the requirement that for every z∈R+
and ∆∈R++ we have u(z+∆, z+∆)>u(z, z). In combination with strict m-monotonicity, strict
equal-material-payoff-monotonicity essentially rules out extreme forms of spite by putting
an upper bound on the malevolence of the DM along the ray m=o. As is easily checked,
almost all (modeling) variants of distributional preferences discussed in the economics
literature satisfy Assumptions 1–4, notable exceptions being lexself preferences
(discussed by Fisman et al., 2007) which – in a strict interpretation – violate the
continuity part of Assumption 1, and maximin (or Rawlsian, or Leontief) preferences
(discussed by Andreoni and Miller, 2002; Charness and Rabin, 2002; or Engelmann and
Strobel, 2004, for instance) which – in their purest form (but not in the form typically
discussed in the literature) – violate strict m-monotonicity.15

<h>CLASSIFICATION OF DISTRIBUTIONAL PREFERENCES: DELINEATION OF TYPES AND THEIR CORE FEATURES</h>
--------------------------------------------------------------------------------

This section introduces a simple graphical classification of distributional preferences
based on the four assumptions introduced in the previous section. Referring to Fig. 1, the
preference of a DM is classified by characterizing the indifference curve that runs
through the reference point r=(e, e). The choice space is divided into six relevant
subsets, {x1, x2, x3} and {y1, y2, y3}. Here, y1 is the area below the 45° line and to the
left of the vertical line through the reference point, y2 is the section of the vertical
line that lies below the reference point, and y3 is the area to the right of the vertical
line and below the horizontal line through the reference point. The subsets {x1, x2, x3}
are defined similarly. Note that Assumptions 2 and 4 together imply that the indifference
curve that runs through the reference point cannot pass through any of the two shaded
areas in Fig. 1. The preference type of the DM is now classified by the subsets that
contain the DM’s indifference curve that runs through r=(e, e). Given Assumptions 1–4, one
section of the indifference curve necessarily runs through one (and only one) of the x
subsets, while the other section necessarily runs through one (and only one) of the y
subsets. Therefore, it is simple to see that there are nine possible archetypes of
distributional preferences given the proposed division in subsets. The nine archetypes are
defined in Table 1 and a typical indifference curve of each archetype is displayed in Fig.
2. Let me shortly discuss the core features of different distributional preference types
rattling around in the literature and how they fit into the proposed template. First
consider selfish or own-money-maximizing preferences. They can be considered as a
degenerated version of distributional preferences where an agent’s well-being neither
increases nor decreases in the monetary payoffs of other agents. Thus, the core property
of selfish preferences in a two-person context is that indifference curves in (m, o) space
are vertical. Referring to Fig. 1 this means that a selfish DM’s indifference curve
through r=(e, e) must run through the subsets x2 and y2 (as indicated in Table 1). The
well-being of an altruistic agent increases in the monetary or utility payoffs of other
agents (Becker, 1974; Andreoni and Miller, 2002); the well-being of an efficiency loving
or surplus maximizing agent (Engelmann and Strobel, 2004), the well-being of an agent with
perfect substitutes preferences (Andreoni and Miller, 2002) and the well-being of an agent
with social welfare preferences (Charness and Rabin, 2002; Fisman et al., 2007) increases
in the (weighted or unweighted) sum of payoffs. In all cases, well-being increases in o
everywhere. Thus, indifference curves in (m, o) space are negatively sloped everywhere (if
o increases m has to decrease to hold the agent indifferent) meaning that (in terms of
Fig. 1) the indifference curve of an altruistic DM must pass through x1 and y3. An agent
is spiteful (Levine, 1998), or competitive (Charness and Rabin, 2002), or status seeking
or interested in relative income (Duesenberry, 1949), if her well-being decreases in the
payoffs of others everywhere; so the core property of such preferences is positively
sloped indifference curves in (m, o) space. In terms of Fig. 1 this means that a spiteful
DM’s indifference curve through r=(e, e) must run through the subsets x3 and y1. The well-
being of an envious or grudging agent decreases in the payoffs of agents who have more,
but is unaffected by the payoffs of agents who have less (the role of envy has been
emphasized by Bolton, 1991 and Mui, 1995, for instance); thus, the core property of
envious preferences is positively sloped indifference curves in the domain of
disadvantageous inequality and vertical indifference curves in the domain of advantageous
inequality (yielding the combination x3, y2).16 The well-being of an agent with maximin
preferences (Engelmann and Strobel, 2004), Rawlsian preferences (Charness and Rabin,
2002), or Leontief preferences (Andreoni and Miller, 2002; Fisman et al., 2007) increases
in the lowest of all agents’ payoffs. Thus, its defining feature in a two-person context
is that indifference curves in (m, o) space are negatively sloped if inequality is
advantageous and vertical otherwise (yielding the combination x2, y3). An agent is
inequity or inequality averse (Fehr and Schmidt, 1999; Bolton and Ockenfels, 2000), or
difference averse (Charness and Rabin, 2002; Fisman et al., 2007), or egalitarian (Dawes
et al., 2007; Fehr et al., 2008) if she incurs a disutility when other agents have either
higher or lower payoffs (as in the model by Fehr and Schmidt, 1999), or when the agent’s
payoff differs from the average payoff of all agents (as in Bolton and Ockenfels, 2000).
Consequently, the defining feature of inequality averse or egalitarian preferences in a
two-person context is negatively sloped indifference curves in the domain of advantageous
and positively sloped indifference curves in the domain of disadvantageous inequality
(yielding the combination x3, y3). The opposite constellation, benevolence in the domain
of disadvantageous inequality combined with malevolence in the domain of advantageous
inequality, is referred to as equality aversion (by Hennig-Schmidt, 2002, for instance),
or as equity aversion (e.g. by Charness and Rabin, 2002 and by Fershtman et al., 2012).
Its defining feature in a two-person context is that indifference curves in (m, o) space
are positively sloped below and negatively sloped above the 45° line (translating to x1,
y1). Table 1 lists and Fig. 2 displays two further archetypes of distributional
preferences, “kick down” and “kiss up”. Those types have not been discussed in the
literature and are included for completeness only: Kick-down or bully-the-underlings
preferences imply malevolence towards agents who have lower and neutrality towards agents
who have higher payoffs. Thus, the defining feature of such preferences in a two-person
context is that indifference curves in (m, o) space are positively sloped in the domain of
advantageous inequality and vertical in the domain of disadvantageous inequality (implying
the combination x2, y1).17 The opposite constellation, benevolence towards agents who are
better off combined with neutrality towards those who are worse off, is called kiss-up or
crawl-to-the-bigwigs preferences and such preferences imply negatively sloped indifference
curves in the domain of disadvantageous inequality and vertical indifference curves in the
domain of advantageous inequality (implying the combination x1, y2). Note that the nine
types listed in Table 1 and displayed in Fig. 2 are well delimitated, mutually exclusive
and comprehensive. Also note how the four basic assumptions introduced earlier enter the
picture: ordering and continuity translate into existence and uniqueness of indifference
curves through any point in (m, o) space; strict m-monotonicity means that upper contour
sets are to the right of an indifference curve (the arrows in Fig. 2); piecewise
o-monotonicity requires that the general attitude of the DM (i.e., whether she is
benevolent, neutral or malevolent) changes at most once – when crossing the equal-
material-payoff line; and strict equal-material-payoff-monotonicity excludes indifference
curves that fall on only one side of equal-material-payoff line. Thus, Assumptions 1–4
together naturally result in the distinction between the nine mutually exclusive and
comprehensive archetypes listed in Table 1 and displayed in Fig. 2, meaning that
qualitatively there is no room left for additional types.18 Before proceeding it seems
important to address the potential critique that the nine archetypes defined here are not
really new. This is correct, of course. The main contribution of the present paper is not
to introduce new preference types; one of the goals is rather to derive the number and
core properties of preference types from a small set of primitive assumptions on
preferences. This stands in contrast to previous studies which either start with a given
list of types or a specific model of preferences. A second – related – critique is that a
list of archetypes similar to the one presented in Table 1 could also be obtained by
working off the possible sign combinations of the two parameters in the piecewise linear
model originally introduced by Fehr and Schmidt (1999) as a description of self-centered
inequality aversion and later extended by Charness and Rabin (2002) to allow for other
forms of distributional concerns. If one is willing to assume that subjects have
preferences of this very specific form then this critique is justified. However, a major
point in the current paper is exactly that there is no need to impose such a tight
structure. This is true both for the type delineation introduced in this and the
elicitation procedure proposed in the next section. Stated differently, all modeling
variants of distributional preferences satisfying the four assumptions introduced in
Section 2 and all distributional archetypes tested for in previous experiments fall into
one of the nine categories defined here. This is also true for the Charness and Rabin
model. On the other hand, there are many models of distributional preferences in the
economic literature that do not fit into the piecewise linear framework of Charness and
Rabin – the altruism models by Andreoni and Miller (2002), Cox et al. (2007) and Cox and
Sadiraj (2012), the envy model by Bolton (1991), and the inequality aversion model by
Bolton and Ockenfels (2000) are prominent examples.

<hs>  Idea of the Equality Equivalence Test</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As mentioned earlier, the four basic assumptions introduced in Section 2 not only
naturally result in a classification of distributional preference types that nests all
major behavioral types discussed in the literature, but also give rise to a clean
identification procedure (a “test”) that does not rely on unnecessary structural
assumptions. This subsection explains how the test works and motivates its name (Equality
Equivalence Test). Given Assumptions 1–4, the DM’s type can be determined by identifying
the location of the two sections of her indifference curve through the reference
allocation r=(e, e), the section that passes the domain of disadvantageous inequality (the
area above and to the left of the 45° line through the reference point) and the section
that passes the domain of advantageous inequality (the area below and to the right of the
45° line). Theoretically, this can be done by exposing the DM to only four binary choices.
Take points r, p1 and p2 in Fig. 3. Suppose we ask the DM to decide subsequently between
p1 and r and between p2 and r. If the DM decides for the p allocation in both choices then
she reveals p1≽r and p2≽r; thus, for the domain of disadvantageous inequality her
indifference curve through r=(e, e) must run through x1. Similarly, if the DM reveals r≽p1
and p2≽r (by deciding for r in the first binary choice and for p2 in the second) then her
indifference curve is in x2.19 And if the DM reveals r≽p1 and r≽p2 (by deciding for r in
both choices) then her indifference curve is in x3.20 By exposing the DM in addition to
binary choices between r=(e, e) and two points on the horizontal line below r (one to the
left and one to the right of the vertical line through r) the location of the second part
of her indifference curve through r – that is, the part that lies below the 45° line – can
be determined. This is the idea behind the EET. Note that the test proposed here is in
many respects similar to the Certainty Equivalence Test (CET) used in experimental
economics (and beyond) as a means to elicit risk attitudes (see Dohmen et al., 2010 for a
recent application). With both procedures the DM is exposed to a short sequence of binary
decision-making problems, where one of the two options is held constant across the binary
choices. In the CET the recurring option is a coin-flip lottery (that is, a lottery with
two possible outcomes occurring with the same probability) and the option that changes
across choices is a safe amount of money. If the researcher is only interested in
qualitative information about the risk attitude of a subject, then exposing her to just
two binary choices – one in which the safe amount of money is just below the expected
value of the lottery and another in which it is just above – is sufficient: If the subject
decides for the lottery in both cases she is classified as risk-loving, if she decides for
the lottery in the former choice and for the safe amount in the latter then she is
classified as risk-neutral, and if she decides for the safe amount in both choices then
she is classified as risk averse. This is very similar to the minimalist version of the
EET described above, the main difference being that in the latter the attitude of the DM
has to be elicited for two domains, for the domain of advantageous inequality and for the
domain of disadvantageous inequality. An implication of this latter difference is that the
minimum test size of the EET is four binary choices, while the minimum test size of CET is
just two binary choices. The minimal version of the CET (as described in the previous
paragraph) gives only qualitative information about the risk attitude of the DM (it
discriminates only between three types of DM – risk-averse, risk-neutral and risk-loving,
where risk-neutrality cannot be identified exactly but only “with arbitrary precision”),
just as the minimal version of the EET described previously gives only qualitative
information about the distributional attitude of the DM (it discriminates only between the
nine archetypes of distributional concerns listed in Table 1, where vertical parts of an
indifference curve cannot be identified exactly but only “with arbitrary precision”). The
standard implementation of the CET differs from the minimal version described above in two
respects: First it exposes subjects to more than one binary choice where the safe amount
of money is higher (lower, respectively) than the expected value of the lottery; and
secondly it includes one binary choice where the safe amount exactly equals the expected
value of the lottery. The symmetric basic version of the EET (to be introduced in the next
subsection) shares these two features: In terms of Fig. 3 (and focusing on the domain of
disadvantageous inequality) it exposes subjects (i) to more than one choice between an
option with the qualitative feature of p1 (p2, respectively); and (ii) to one choice where
the alternative to the recurring reference point is located exactly on the intersection of
the horizontal line above the reference point and the vertical line through the reference
point. With both tests the aim of the former modifications (in comparison to the minimal
version) is to get information about preference intensity while the latter modification is
intended “to give a sign to neutrality” (see below). The overall goal of the CET is to
identify the safe amount that generates indifference to a given gamble. With a list of
binary choices the point of indifference cannot be identified exactly. However, by keeping
the lottery constant and increasing the safe amount systematically from one choice to the
next the researcher can identify the “switching point” of the subject, i.e., the binary
choice where the subject switches from the lottery to the safe alternative. This switching
point gives a range for the point of indifference and thereby for the certainty equivalent
of the subject to the given lottery. Suppose a subject decides for the lottery in all
choices where the expected value of the lottery is higher than the safe amount and for the
safe amount in all choices where it is lower. Then the behavior of the subject is
consistent with risk neutrality. However, it is also consistent with a low degree of risk
aversion and with a low degree of risk loving. By exposing the subject in addition to a
choice where the safe amount corresponds to the expected value of the lottery the
researcher “attaches a sign to risk neutrality”. The overall goal of the EET is the
identification of the locations of two points of indifference to the reference allocation,
one for the domain of advantageous inequality, the other for the domain of disadvantageous
inequality. With a list of binary choices the points of indifference cannot be identified
exactly. However, by keeping the symmetric reference point and the material payoff of the
other person in the asymmetric allocation constant across binary choices (in a given
domain) and increasing the material payoff of the DM systematically from one choice to the
next the researcher can identify the “switching point” of the subject in the respective
domain, which gives a range for the point of indifference of the DM in the domain under
scrutiny.21 As will be shown in Section 4.3, this information can be used to construct a
two-dimensional index representing both the archetype of distributional concern and the
preference intensity (conditional on the chosen vertical distance between r and the
horizontal line). Suppose a subject decides for the symmetric reference point in all
choices where her material payoff in the reference allocation is higher than her payoff in
the asymmetric allocation and for the asymmetric allocation in all choices where it is
lower. Then the behavior of the subject (in the domain under investigation) is consistent
with selfishness. However, it is also consistent with a low degree of benevolence and with
a low degree of malevolence. By exposing the subject in addition to a binary choice where
her payoff is the same in the reference point and in the asymmetric allocation, we elicit
her impartial distributional preference thereby “attaching a sign to selfishness”.22 Given
the many similarities between CET and EET it probably does not come as a surprise that the
two also share many pros and cons (in comparison to econometric elicitation techniques).
The main advantages of the two tests are (i) that they are simple and short as they merely
require subjects to complete a comparatively short sequence of binary decision making
problems, properties that facilitate comprehension by experimental subjects and serve the
experimenter’s need to limit the duration of experimental sessions; (ii) that they are
parsimonious as they rely on a small set of comparatively mild primitive assumptions on
preferences; (iii) that they are general as they directly tests the core features of
preferences rather than concrete models or functional forms; (iv) that they are flexible
as test size and test design can easily be fine-tuned to the research question of
interest; (v) that they are precise because they identify the preference type with
arbitrary precision and also give an index of preference intensity; and (vi) that they
minimize experimenter demand effects as subjects are asked to make binary decisions in a
neutral frame and do not have the option to do nothing. The main disadvantages of the two
tests in comparison to econometric elicitation techniques are (i) that the switching
point(s) of a subject give(s) only a range for the point(s) of indifference, which implies
that “neutrality” cannot be identified exactly but only “with arbitrary precision”; (ii)
that the assumptions on which the approaches rely are not directly tested; (iii) that the
index of preference intensity for a given subject and the distribution of types that is
inferred from a sample of subjects depend on the chosen parameterization of the test; and
(iv) that they provide no measure of uncertainty of a subject’s elicited preference type.
We discuss this latter issue further in Section 4.5.

<hs>  The symmetric basic version of the Equality Equivalence Test</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As explained above the EET exposes subjects to a series of diagnostic binary choice
problems. In the (symmetric) basic version of the test the family of binary choices is
characterized by four positive integers, e, g, s and t, where e determines the locus of
the equal-material-payoff allocation (m, o)=(e, e); g is a “gap” variable characterizing
the vertical distance between (e, e) and the two horizontal lines in Fig. 3 (see Fig. 4);
in order to avoid zero or negative monetary payoffs we restrict g to values strictly
smaller than e; s is a “step size” variable characterizing the horizontal distance between
two adjacent points on a line; t≥1 is a “test size” variable determining the number of
steps (of size s) which are made to the left and to the right starting from the point just
above or below (m, o)=(e, e); in order to preserve advantageous and disadvantageous
inequality we impose the restriction t≤g/s. In total the symmetric basic version of the
EET consists of 4t+2 binary decision problems. In each decision problem the subject is
asked to decide between two alternatives (named Left and Right), each involving a payoff
pair – one payoff for the subject (the DM) and one for the (randomly matched, anonymous)
other subject (the passive person). For expositional purposes the decision problems are
separated into two blocks, the disadvantageous inequality block (X-List) and the
advantageous inequality block (Y-List). Within each block the decision problems are
presented as rows in a table. In each decision problem one of the two alternatives (the
alternative “Right”, say) is the (recurring) equal-material-payoff allocation (m, o)=(e,
e). For the disadvantageous inequality block the second alternative in each decision
problem (the alternative “Left”) is constructed as shown in Table 2. The construction of
the second alternative for the advantageous inequality block is similar, the only
difference being the material payoff of the passive person for the alternative LEFT, which
is now e−g (instead of e+g). An important feature of the EET is that within each of the
two blocks the material payoff of the passive person in the asymmetric allocation is held
constant, while the material payoff of the DM increases monotonically from one choice to
the next. Together with the fact that the symmetric allocation remains the same in all
choices, this design feature guarantees that strict m-monotonicity is enough to make sure
that when facing the choice between Left and Right within a given block, each individual
switches at most once from Right to Left (and never in the other direction). In Section
4.4 I will use the two switching points of a subject to construct a two-dimensional index
representing both archetype and intensity of distributional concerns (conditional on the
chosen test parameters – see Section 4.5 for a discussion). As previously mentioned the
EET allows for discrimination between the nine archetypes at any arbitrary precision. More
specifically, the researcher needs to define when an agent should be considered as
egoistic in a particular domain (this is the meaning of arbitrary precision). Suppose we
define an agent to be egoistic in a particular domain if she is not willing to give up c
Cents in order to change the material payoff of the passive person by 1$. Then the
appropriate EET has to be such that c=100s/g⇔s=cg/100 meaning that we can choose the
remaining parameters of the test freely.

<hs>  Extending and refining the Equality Equivalence Test</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The working paper version of this article (Kerschbamer, 2013) proposes three modifications
of the symmetric basic version of the test that might help to shed light on more specific
research questions. The first modification replaces the symmetric step-size in the basic
version by an asymmetric one (where the step size is small at the center but grows larger
when moving away from the center) in order to increase the power of the test to
discriminate between selfish and different variants of non-selfish behavior without
increasing the size of the test or decreasing the discriminatory power of the test at the
borders. The second modification extends the X-List to the left and the Y-List to the
right in order to address the question whether there are subjects who (in the relevant
range) put more weight on the material payoff of the passive person than on their own
material payoff. The third modification is a multi-list version of the EET where subjects
are asked to complete two or more X- and Y-lists distinguished by the size of the gap
variable g. This modification is intended to gain more insights on the exact shape of
indifference curves in (m, o)-space.

<hs>  Identifying archetype and characterizing intensity of distributional concerns: the (x, y)-score</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

This subsection describes a method to identify the archetype and to characterize the
intensity of the distributional preference of a subject based on her choices in the
symmetric basic version of the test. It then proposes a procedure to represent the type-
intensity distribution of a given subject pool graphically. Step 1 (consistency check): As
argued above an individual whose preferences satisfy strict m-monotonicity has at most one
switch from Right to Left (and no switch in the other direction) in each of the two
tables. Step 1 is to eliminate all subjects that fail this basic consistency check (in an
implementation of the symmetric basic version of the test – see Section 5 for details –
less than 5% of the subjects failed the consistency check). Step 2 (defining scores):
Represent each subject with consistent behavior by an (x, y) tuple defined as follows: The
variable x (x-score) summarizes the behavior of the individual in the disadvantageous-
inequality related block (X-List) and is defined as (t+1.5) points minus the row number in
which the individual decides for the first time for the asymmetric allocation (that is,
for the payoff vector on the left hand side). If an individual always decides for the
symmetric (or egalitarian) allocation, we take the convention that she decides for the
first time for the asymmetric allocation in the (2t+2)th row, so that she gets an x-score
of −(t+0.5). For instance, if in the test version displayed in Fig. 4 (where t=2) an
individual decides for the symmetric allocation in the first row of the X-List and for the
asymmetric allocation in the second (and in all other) row(s) then she gets an x-score of
3.5–2=1.5. The variable y (y-score) summarizes the behavior of the subject in the
advantageous-inequality related block (the Y-List) and is defined as the row number in
which the individual decides for the first time for the asymmetric allocation minus
(t+1.5) points. If an individual always decides for the symmetric allocation, we take
again the convention that she decides for the first time for the asymmetric allocation in
the (2t+2)th row; she then gets a y-score of t+0.5. Note that the definition of the two
scores implies that each of them can take on 2(t+1) different values (see Table 3); thus,
the proposed test allows for 4(t+1)² different (x, y)-scores. Also note that a positive
(negative) x-score corresponds to benevolence (malevolence) in the domain of
disadvantageous inequality, while a positive (negative) y-score corresponds to benevolence
(malevolence) in the domain of advantageous inequality. Furthermore, the magnitude of the
x-score (y-score, respectively) is an ordinal index of the intensity of distributional
preferences in the domain of disadvantageous inequality (advantageous inequality,
respectively).23 Step 3 (representing relative frequencies of types): Represent the
absolute or relative frequencies of the different (x, y)-scores in an axis of abscissas as
shown in Fig. 5.

<hs>  Relation of (x, y)-score to parameters in piecewise linear model and to WTP</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Note that the piecewise linear model implies that the DM’s willingness to pay (WTP) for
income increases (or decreases) of the passive person is piecewise constant (WTP=uo/um,
where the subscripts denote partial derivatives). In the domain of disadvantageous
(advantageous) inequality we have WTPd=σ/(1−σ) (WTPa=γ/(1−γ), respectively); if σ≥0 (γ≥0,
respectively) then this term gives the own-money amount the DM is willing to give up in
the domain of disadvantageous inequality (advantageous inequality, respectively) in order
to increase the other person׳s material payoff by a single unit; symmetrically, if σ<0
(γ<0, respectively) then −σ/(1−σ) (−γ/(1−γ), respectively) gives the own-money amount the
DM is willing to give up in the domain of disadvantageous inequality (advantageous
inequality, respectively) in order to decrease the other person׳s material payoff by a
single unit. Thus, within the piecewise linear model x-scores translate into WTPd as shown
in the right-most column of Table 4 (again the translation for the y-score is similar
except that WTPd is replaced by WTPa and strict inequalities are replaced by weak ones).
It is important to note that using estimates of the parameters of the piecewise linear
model (or estimates of the piecewise constant WTP for changes in the income of the other)
as a cardinal metric for distributional preferences does not necessarily mean assuming
piecewise linear preferences: In experimental set ups, where stakes tend to be small, the
estimates are probably best interpreted as linear approximations of the true values. This
interpretation is especially valid when the parameters of the piecewise linear model are
estimated from the raw data using the McFadden (1974) random utility specification. In
addition to yielding a cardinal metric that is comparable across studies, estimating the
parameters of such a structural model has several other practical advantages as well:24 As
McFadden׳s random utility specification allows for noisy decisions, subjects with
inconsistent choices do not have to be dropped. This may be crucial when a test design
with high resolution (i.e. with large gap variable g and small step size s) is used, or
when the binary choices are presented to the subjects one-at-a-time in random order (see
Appendix A for a discussion of implementation issues). The parameters׳ standard errors
enable statistical tests; for example, to check whether a subject׳s deviations from purely
selfish behavior are statistically significant. The structural model could also be applied
in the context of a finite mixture specification. This would allow the experimenter to
identify the prevalent social preference types and to endogenously classify each subject
into the type that fits her behavior best. The parameters of the piecewise linear model
can also be estimated when the test is applied in its multi-list variant (introduced in
Kerschbamer, 2013) where the (x, y)-score is no longer available.

<h>EXPERIMENTAL RESULTS BASED ON THE SYMMETRIC BASIC VERSION OF THE EET</h>
--------------------------------------------------------------------

Here the data from a paper-and-pen experiment based on the symmetric basic version of the
test is reported. The experiment was conducted in paper-and-pen (and several other design
features reported below were applied) to convince subjects that neither other experimental
subjects nor the experimenters could identify the person who has made any particular
decision. This was done in an attempt to minimize the impact of experimenter demand and
audience effects. See List (2007) for a discussion on experimenter demand effects and
Hoffman et al. (1994), Andreoni and Petrie (2004), and Andreoni and Bernheim (2009) for
experimental evidence indicating that – depending on the experimental design – audience
effects might have a large impact on subjects׳ behavior in dictator-game like
situations.25

<hs>  Experimental procedures</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

Five experimental sessions were conducted manually (i.e., in pen-and-paper) at the
University of Innsbruck in autumn 2009. Forty subjects who had not participated in similar
experiments in the past were invited to each session using the ORSEE recruiting system
(Greiner, 2004). Since not all subjects showed up in time, 192 (instead of the invited
200) subjects from various academic backgrounds participated in total, and each subject
participated in one session only. After arrival, subjects assembled in one of the two
laboratories and individually drew cards with ID numbers (which remained unknown to other
participants and the experimenters). Then instructions were distributed and read aloud.26
Instructions informed subjects (i) that there are two roles in the experiment, the role of
an “active person” and the role of a “passive person”; (ii) that there is exactly the same
number of active and passive subjects in the experiment and that roles are assigned
randomly; (iii) that each active person is matched with exactly one passive person and
vice versa, and that at no point in time a participant will get to know anything regarding
the identity of the person she/he is matched with; (iv) that active persons are called to
make a series of ten binary decisions that determine not only their own earnings from the
experiment but also the earnings of the passive person they are matched with; (v) that
passive persons do not have a decision to make in the experiment and that their earnings
will depend exclusively on the decisions of the active person they are matched with; (vi)
that only one of the ten choice problems of each active person will be relevant for cash
payments; and (vii) that cash payments could be collected the day after the experiment at
one of the secretaries who also handles the cash payments for other experiments (to ensure
that the amount a subject earns cannot be linked to her/his decisions). Then subjects were
randomly assigned to one of the two roles; active persons stayed in the same room while
passive persons were escorted to the adjacent laboratory. In both rooms subjects were
seated at widely separated computer terminals (computers were switched off) with sliding
walls. Active persons were handed out a form consisting of two pages – an empty cover
sheet and a decision sheet as described in the next paragraph – and they were asked to
fill out the decision sheet in private. Passive persons received a form consisting of
three pages – an empty cover sheet and a two-page questionnaire unrelated to the
experiment – and they were asked to complete the questionnaire in private. After the tasks
in both rooms had been completed, for each active person one of the choice problems was
randomly selected via a manual device – a bingo ball cage handled by the active person –
for the purpose of cash-payment generation. The payoff-relevant decision problem was
written on the cover page of the active person and the person was given the opportunity to
take (in private) a look at her/his choice in the payoff-relevant decision problem. Now
subjects in both rooms were asked to label (in private) the cover sheet of their document
with their ID number. Then participants in both rooms were called to put their documents
(again in private) in boxes before leaving the room. Anonymous cash payments started the
next day – giving experimenters the opportunity to manually match active with passive
persons in the meantime. Participants presented the card with their ID number to an admin
staff person, who did not know who did what for which purpose nor how cash payments were
generated, and they got their earnings in exchange (the fact that cash payments would be
made that way was clearly indicated in the instructions). On average subjects earned
approximately 11 Euros plus a show up fee of 4 Euros.

<hs>  Experimental design</hs>
  ~~~~~~~~~~~~~~~~~~~

The symmetric basic version of the test was implemented with e=10, g=3, s=1, t=2 and with
experimental currency units corresponding to Euros. Thus, each active person (96 in total)
was exposed to 10 binary decision problems with (10, 10) as the recurring equal-material-
payoff allocation. The decision problems were presented in two tables, 5 in the X-Table
(disadvantageous inequality) and 5 in the Y-Table (advantageous inequality). The design of
the two tables was similar to that of Table 2.

<hs>  Discussion</hs>
  ~~~~~~~~~~

The experiment reported here uses the fixed-role-assignment protocol, where roles (active
DM and passive person) are assigned ex ante, and only active DMs decide while passive
persons do nothing. While this protocol seems to be the cleanest one from a theoretical
point of view, it is not practicable when the test is intended as a tool to be added to
arbitrary other experiments, since the preferences of half of the subjects remain
unclassified. An easy way to have a measure of all subjects׳ social preferences is to
either use the role-uncertainty protocol (where each subject decides in the role of the
active DM, and only later subjects get to know whether their decision is relevant – as in
Engelmann and Strobel, 2004 and in Blanco et al., 2011, for instance), or the double-role-
assignment protocol (where each subject decides, and each subject gets two payoffs, one as
an active DM and one as a passive person – as in Andreoni and Miller, 2002 and in Fisman
et al., 2007, for instance). Appendix A discusses some pros and cons of the different
protocols. A second issue worth discussing regards the implemented test version. The
experiment reported here uses the symmetric basic version of the test (which has
equidistant step sizes in the binary choice lists) with a relative low resolution (i.e., a
relatively high value of the quotient s/g). As is evident from the results, however, this
form of the test yields a classification that is coarser than some researchers might find
ideal. To address this issue, either an asymmetric test version with small step sizes in
the center and larger step sizes in the periphery (as suggested in Section 4.3) could be
used, or the power of the symmetric version of the test to discriminate between selfish
and different variants of non-selfish behavior could be increased by increasing g, keeping
the rest of the test as it is (remember the discussion on “identification with arbitrary
precision” in Section 4.2). A third implementation issue regards the presentation of
tasks. In the paper-and-pen experiments reported here the binary decision tasks were
presented to the subjects in ordered lists (similar to the lists often used in risk-
attitude elicitation tasks). In computer-aided experiments presenting the binary decisions
one-at-a-time in random order (i.e., each binary decision on an own screen) might be an
attractive alternative. Appendix A discusses this issue further. A final point worth
addressing regards the comparison of subjects according to the intensity of preferences.
The implemented standard version of the test uses only one size of g. If subjects differ
in the shape of indifference curves, their relative ranking regarding preference intensity
may depend on g. For instance, one person might be more altruistic than another if g is
small, but less altruistic than the other if g is large. More generally, if distributional
preferences are non-linear, any results regarding the relationship between intensity of
distributional preferences and behavior in another experiment will depend to some degree
on the level of g chosen for the test. So, if a researcher is interested in correlating
the intensity of benevolence or malevolence in the two domains (i.e., the x- and the
y-score) with behavior in another experiment it seems advisable to adapt the parameters of
the test to the parameters in that other experiment.

<h>CONCLUSIONS</h>
-----------

This paper has proposed a geometric delineation of distributional preference types and a
non-parametric approach for their identification in a two-person context. Major advantages
of the proposed Equality Equivalence Test (EET) over previous ones are (i) that it is
simple and short as subjects’ task is to make a small set of diagnostic choices without
feedback; (ii) that it is parsimonious as it relies on a small set of primitive
assumptions; (iii) that it is general as it directly tests the core features of different
types of distributional preferences rather than concrete models or functional forms; (iv)
that it is flexible as test size and test design can easily be fine-tuned to the research
question of interest; (v) that it is precise as it identifies the archetypes of
distributional concerns with arbitrary precision and also gives an index of preference
intensity; and (vi) that it minimizes experimenter demand effects as subjects are asked to
make binary decisions in a neutral frame and do not have the option to do nothing.30 Those
features together suggest that the EET might be suitable as a tool in experimental
economics to disentangle the impact of distributional preferences from that of other
factors thereby helping to interpret data from other (unrelated) experiments (similar to
the choice list tests used to elicit risk attitudes; see Holt and Laury, 2002, or Dohmen
et al., 2010, 2011).31 That the EET is indeed suitable for that purpose has been shown in
two recent studies: Balafoutas et al. (2012) investigate in a standard lab experiment the
relationship between distributional preferences and competitive behavior and find (a) that
distributional archetypes (as assigned by the proposed test) differ systematically – and
in an intuitively plausible way – in their response to competitive pressure, in their
performance in a competitive environment and in their willingness to compete; and (b) that
controlling for the effects of distributional preferences, as well as for risk attitudes
and some other factors, closes the large gender gap in competitive behavior found in
earlier studies (by Niederle and Vesterlund, 2007, 2010, for instance). This is an
important finding because it indicates that the gender gap in competitiveness is largely
driven by mediating factors (potentially accessible to policy intervention) and not by
gender per se. Hedegaard et al. (2011) examine in a large-scale internet experiment the
impact of distributional concerns on the contribution behavior in a standard (linear)
public goods game and find (a) that distributional archetypes differ systematically – and
in an intuitively plausible way – in their contribution behavior; and (b) that accounting
for the differences explains roughly half of the gap between actual behavior of subjects
in the lab and the theoretical benchmark derived under the assumption that players are
rational and selfish (and that this fact is common knowledge). Again, this is an important
finding because it helps to disentangle the impact of distributional concerns on the
behavior of subjects in social dilemma games from that of other factors – as beliefs on
others׳ behavior or intentions, for instance. Together the findings in those studies
clearly indicate that associating subjects with one of the proposed archetypes of
distributional concerns has explanatory value and that the proposed test is indeed a valid
control instrument in experimental economics. Given that the EET does not provide a
measure of uncertainty of a subject’s classification (in the sense of a counterpart of the
standard error of an estimated parameter of a structural model), a systematic
investigation of the test–retest reliability of the EET would be an interesting area of
future research. The results of a recent study suggest that this reliability is high:
Balafoutas et al. (2014) compare experimentally the revealed distributional preferences of
individuals and teams by exposing subjects to the EET under two different decision-making
regimes: an individual regime and a team regime. The authors employ a mixed within- and
between-subjects design in two sets of sessions run in two consecutive weeks: In the first
week all subjects are exposed to the EET in the individual regime; in the second week some
subjects are again exposed to the individual regime, while the rest make their choices in
the EET in the team regime. This design feature allows addressing the test–retest
reliability issue by comparing the choices of subjects who face the individual regime
twice across the two weeks. The authors show (in Table 5) that elicited preference types
remain remarkably stable over the two weeks. Beyond its potential to act as a control
instrument in experimental economics, other potentially fruitful applications of the EET
include (a) investigating the stability of distributional preferences over different
domains (for instance, a potential shortcoming of the approach proposed here is its focus
on the two-agents case; investigating whether the preferences revealed in that context
carry over to a richer environment is surely an important issue);32 (b) investigating
possible links between distributional preferences and other forms of other-regarding
preferences (for instance, “Are altruists more or less likely to be motivated by positive
or negative reciprocity?”, “Do altruism and altruistic rewarding (or altruistic
punishment) go together or are they mutually exclusive ways to reach the same goal –
promoting private provision of public goods?” 33, or “Is the test-based classification of
subjects in distributional-preference types somehow correlated with the propensity to be
motivated by trust?”) ;34 and (c) applying the EET (together with tests for risk and time
preferences and for personality traits) in experiments with large demographic variation
(age, gender, income, education) or with a representative sample of the population to
detect patterns and correlations (for instance, “Are distributional preferences and risk
attitudes or time preferences somehow related?”, “Are there gender differences in the
distribution of archetypes?”35 or “What is the impact of age and income on distributional
preferences?”). Beyond economics the proposed test might help to address important
research questions in biology and psychology as, for instance, “What determines human
altruism (or spite)?” or, “What drives altruistic punishments and rewards?”. For those and
many other interesting research questions, identification of distributional preference
types in a “clean” environment appears to be a natural first step. The proposed EET seems
to be well suited for this purpose. Turning back to the quote at the start of the paper
the hope is that it turns out to be “as simple as possible, but not one bit simpler”.


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<ART>The impact of a carbon tax on manufacturing: Evidence from microdata
====================================================================

Authors: Ralf Martin, Laure B. de Preux, Ulrich J. Wagner
DOI: 10.1016/j.jpubeco.2014.04.016
Year: 2014  |  Pages: 1-14
ASJC codes: 2002, 2003
Keywords: Carbon tax, Climate change levy, Energy use, Manufacturing, Policy evaluation, UK

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We estimate the impact of a carbon tax on manufacturing plants using panel data from the UK production census. Our identification strategy builds on the comparison of outcomes between plants subject to the full tax and plants that paid only 20% of the tax. Exploiting exogenous variation in eligibility for the tax discount, we find that the carbon tax had a strong negative impact on energy intensity and electricity use. No statistically significant impacts are found for employment, revenue or plant exit. © 2014.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The rise of climate policy on government agendas around the world has stirred a renewed
interest in the optimal design of large-scale regulation of environmental externalities.
Climate change – the “ultimate commons problem” (Stavins, 2011) – is caused by
anthropogenic emissions of greenhouse gases (GHG) such as carbon dioxide (CO2) and is
expected to have severe ecological and economic consequences (IPCC, 2007). Mitigating
climate change will require substantial abatement of GHG emissions from all core economic
sectors (Pacala and Socolow, 2004). The choice of appropriate policy instruments for each
of these sectors is essential for minimizing the overall economic costs of mitigation with
given technologies (static efficiency), and for stimulating technological innovations that
will further reduce mitigation costs in the future (dynamic efficiency). This paper
evaluates the performance of one such instrument, a tax designed to curb industrial CO2
emissions, in a panel of manufacturing plants. Manufacturing is a major contributor to GHG
emissions around the world.1 Since most manufactured goods are tradable, there is a risk
that regulated firms will lose international competitiveness, shed part of their labor
force or even exit. These concerns have been fueling vehement opposition towards
regulation and left their mark on the design of the policies implemented so far. Command-
and-control policies have long been the predominant form of environmental regulation in
the manufacturing sector, and their impacts have been studied extensively in the context
of air pollution.2 On theoretical grounds, economists have favored market-based
instruments such as taxes and tradable permit schemes because they are more efficient in
both the static and dynamic senses (e.g. Montgomery, 1972; Milliman and Prince, 1989;
Tietenberg, 1990). However, empirical evidence on the impacts of market-based
environmental regulation on manufacturing is scarce, especially when it comes to carbon
emissions.3 For example, the European Union Emissions Trading Scheme (EU ETS), the largest
cap-and-trade system for carbon emissions worldwide, is overdue for a microeconometric
evaluation (Martin et al., 2013b). While carbon taxes have been implemented in various EU
countries, their rigorous evaluation has proven difficult, be it because of the lack of
suitable microdata or because of the lack of a compelling identification strategy.4 This
paper fills the void by analyzing the Climate Change Levy (CCL) package — the single most
important climate change policy that the UK government has unilaterally imposed on the
business sector so far (HM Government, 2006). The package consists of a carbon tax – the
CCL – and a scheme of voluntary agreements available to plants in selected energy
intensive industries. Upon joining a Climate Change Agreement (CCA), a plant adopts a
specific target for energy consumption or carbon emissions in exchange for a highly
discounted tax liability under the CCL. While the CCL package is still in place today, our
analysis focuses on the first three years following its introduction in 2001, thereby
avoiding overlap with the EU ETS. During the period of analysis, the CCL added 15% to the
energy bill of a typical UK business (NAO, 2007) and the discount granted under a CCA
amounted to 80% of the tax rate. Given its scope and institutional context, the CCL
package provides a unique opportunity to study the effects of a carbon tax in an
industrialized economy. We use longitudinal data on manufacturing plants to estimate the
impact of the CCL on energy use, emissions and economic performance. Our identification
strategy is to compare changes in outcomes between fully-taxed CCL plants and CCA plants.
A naïve difference-in-differences (DiD) estimator would likely be biased because the
plants that were eligible for CCA participation could self-select their tax regime.
However, plants were only eligible if they emitted pollutants subject to environmental
regulation pre-dating the CCL. The variation in eligibility across plants can hence be
exploited to instrument for the tax rate. We implement this idea in an IV framework where
the reduced form is a DiD regression of plant outcomes on eligibility. For this approach
to be consistent, it must be true that differences between eligible and non-eligible
plants are not systematically related to changes in outcome variables over the treatment
period. While this assumption is not testable, we show that there are no significant trend
differences between eligible and non-eligible firms in the pre-treatment period. In
addition, we exploit the panel structure of the dataset to control for pre-trends directly
in the regression. Firms in the control group were not only entitled to a tax discount,
but they also faced a reduction target for energy consumption or carbon emissions.
Although these targets could have placed binding constraints on the plant's production
choices, the fact that massive over compliance occurred right from the start suggests
otherwise. In fact, a large degree of flexibility was built into both the target
negotiation process and the compliance review. If targets were nonetheless stringent, then
our estimate represents a lower bound on the full price effect of the tax differential
between the two groups of plants. With this approach, we find robust evidence that the CCL
had a strong negative impact on energy intensity, particularly at larger and more energy
intensive plants. An analysis of fuel choices at the plant level reveals that this effect
is mainly driven by a reduction in electricity use and translates into a negative impact
on CO2 emissions. In contrast, we do not find any statistically significant impacts of the
tax on employment, revenue (gross output) or total factor productivity (TFP). In addition,
we examine extensive-margin adjustments and find no evidence that the CCL accelerated
plant exit. While the regression-based test we use does not have much power to detect
small negative impacts on these outcomes, our results do not substantiate worries about
devastating effects of the CCL on the competitiveness of UK manufacturing, which gave way
to a costly exemption scheme.5 Over the past two decades, carbon taxes and their effects
on industrial competitiveness have been a matter of political debate in many
industrialized countries. By conducting the first ex-post analysis of the causal impact of
such a tax on manufacturing, our study provides much-needed empirical evidence on the
impacts of large-scale regulation aimed at pricing pollution. It does so in the context of
climate change – an area where regulatory stringency is bound to increase in the near
future – and with a focus on manufacturing, the principal engine of growth in the emerging
economies and still a cornerstone of employment in post-industrial economies. The
remainder of the paper is structured as follows. Section 2 describes the CCL package in
detail and reviews previous research on the tax. Section 3 describes the research design
and econometric framework. Section 4 describes the data sources and summarizes the dataset
used for the analysis. Section 5 reports the main results and presents several robustness
checks. Section 6 examines heterogeneous impacts, aggregate effects and estimates the
impact of the CCL on exit. Section 7 concludes.

<hs>  The Climate Change Levy and Climate Change Agreements</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Since the 1990s the UK has adopted a series of increasingly ambitious targets for climate
policy. In addition to a 12.5% reduction of GHG emissions from 1990 levels to be achieved
under the Kyoto Protocol, the Blair administration promised to reduce CO2 emissions by 19%
by 2010 and by 60% by 2050.6 When the CCL package was implemented in 2001, it constituted
the single-most important policy aimed at achieving these goals.7 The CCL is a per unit
tax payable at the time of supply to industrial and commercial users of energy. It was
first announced in March 1999 and came into effect in April 2001. Taxed fuels include
coal, electricity, natural gas, and non-transport liquefied petroleum gas (LPG). For each
fuel type subject to the CCL, Table 1 displays the tax rates per kilowatt hour (kWh)
equivalent, the average energy price in Pound Sterling paid by manufacturing plants in
2001 and the implicit carbon tax. Energy tax rates vary substantially across fuel types,
ranging from 6.1% on coal to 16.5% on natural gas.8 While the tax establishes a meaningful
price incentive for energy conservation overall, it is immediately seen that carbon
contained in gas and electricity is taxed at almost twice the rate as carbon contained in
coal.9 Other fuel types were tax-exempt precisely because of their low carbon content,
such as electricity generated from renewable sources and from combined heat and power.
Hence, rather than a pure carbon tax the CCL is a tax on energy with non-uniform rates,
shaped by a mixed bag of fiscal and regulatory goals. Similar to other European
governments that had introduced energy taxes during the 1990s, the UK government set up a
scheme of negotiated agreements, the CCAs, in order to mitigate possible adverse effects
of the CCL on the competitiveness of energy intensive industries. By participating in a
CCA, facilities in certain energy intensive sectors can reduce their tax liability by 80%
provided that they adopt a binding target on their energy use or carbon emissions. Defined
either in absolute terms or relative to output, these targets were negotiated at two
levels. In an ‘umbrella agreement’, the sector association and the government –
represented at the time by the Department for Environment, Food, and Rural Affairs (DEFRA)
– agreed upon a sector-wide target for energy use or carbon emissions in 2010 and on
interim targets for each two-year compliance period. At a lower level, ‘underlying
agreements’ stipulate a specific reduction to be achieved by a ‘target unit’, i.e. a
facility or group of facilities in a sector with an umbrella agreement. DEFRA originally
negotiated 44 umbrella agreements with different industrial sectors, including the ten
most energy intensive ones.10 While the primary objective of both the CCL and the CCAs is
to enhance the efficiency of energy use in the business sector, the two instruments
represent fundamentally different approaches. The levy provides a price signal at roughly
15% of energy prices faced by the typical business in 2001 (NAO, 2007). If energy demand
is price sensitive, the increased relative price of energy should lead to a reduction in
energy consumption. In terms of CO2 emissions, this effect could be offset in part by a
shift towards more carbon-intensive fuels. In contrast, the CCA combines a very diluted
price signal of 0.2 × 15% = 3% of energy prices faced by the typical business with
quantity regulation, mostly in the form of efficiency targets. This target affects the
plant only if it places a binding constraint on the trajectory of energy use during the
remaining economic lifetime of the plant. If this is not the case, the plant faces weaker
incentives for energy conservation than it would under the full tax rate. Moreover, since
most targets are specified in terms of energy units rather than carbon emissions, there is
no guarantee that even a stringent energy target leads to emission reductions.

<hs>  How stringent are the targets negotiated in the CCAs?</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In theory, an omniscient government can choose a combination of tax discount and reduction
targets so as to induce at least as much abatement as under the full tax rate (Smith and
Swierzbinski, 2007). In reality, however, the government is unlikely to have perfect
information about firm-specific abatement cost, especially if firms worry that sharing
this information with the government weakens their bargaining position in the target
negotiations. What is more, the government might not have been willing to drive a hard
bargain for fear of jeopardizing international competitiveness and exacerbating
distortions in marginal abatement cost (de Muizon and Glachant, 2003; Smith and
Swierzbinski, 2007). A closer inspection of the negotiation, monitoring and enforcement of
CCA targets yields a number of reasons to believe that the targets did not place binding
constraints on firm behavior. First, the government may have “double counted” carbon
savings from the CCA scheme (ACE, 2005). On average, CCA targets were supposed to improve
energy efficiency by 11% between 2000 and 2010. This figure is well above the 4.8%
improvement the government expected to occur under a “business as usual” (BAU) scenario
(AEAT, 2001). However, alternative BAU scenarios were much closer to the CCA target,
projecting energy efficiency of all UK industry to improve by 9.5% (DG Transport and
Energy, 1999) or even 11.5% when taking into account the effect of the CCL (DTI, 2000).
Second, there was massive overcompliance with CCA targets. Combined annual carbon savings
in all CCA sectors were substantially larger than the 2010 target throughout the first
three compliance periods. At the end of the first compliance period in 2002, CCA sectors
reported savings of 4.5 MtC — almost twice the target amount of 2.5 MtC to be achieved by
2010.11 Consistent with this, the proportion of compliant target units was high, rising
from 88% in the first compliance period to 98% and 99% in the second and third compliance
periods, respectively (AEAT, 2004, 2005, 2007). CCA participants that did not meet their
target could attain compliance by buying emission allowances on the UK Emissions Trading
Scheme (UK ETS), a carbon market that was operational between 2002 and 2006. Allowance
prices in this market remained below the implicit carbon tax rates given in Table 1.12
Third, the lower bound on compliance cost is zero. This is because facilities were re-
certified for the reduced tax rate even if they had missed their target, provided that the
sector as a whole met its target. In 2004, this was true of approximately 250 non-
compliant target units (NAO, 2007). Finally, a large degree of flexibility in both the
target negotiations and the compliance review further limited the stringency of CCA
targets. For instance, CCA sectors could choose their own baseline year for the target
indicator. More than two thirds of all sectors chose a baseline year prior to 2000 (in
some cases going as far back as 1990), allowing them to count carbon savings unrelated to
the CCA towards target achievement (NAO, 2007). Furthermore, targets could be adjusted ex
post to reflect a more energy intensive product mix, declining output, or other ‘relevant
constraints’.13 Because of this, and for the reasons given above, it appears unlikely that
the negotiated CCA targets placed binding constraints on energy use by the average CCA
company.14

<hs>  Previous evaluations of the CCL package</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Several evaluations of the CCL package were conducted at different stages of its
implementation. In the 2000 Regulatory Impact Assessment, the government projected that
the CCL instrument alone would achieve carbon savings of at least 2 MtC in 2010 against
BAU projections (HMCE, 2000). This estimate was based on a model of business energy use
maintained by the Department of Trade and Industry (DTI). An interim evaluation study,
commissioned by DEFRA at the end of the second commitment period in 2004, finds evidence
that the announcement of the CCL package in March 1999 reduced energy demand in the
service and public sectors, but not in manufacturing (Cambridge Econometrics, 2005). The
authors of the study identify this “announcement effect” as a structural break in an error
correction model of quarterly energy demand (see Agnolucci et al., 2004, for more
details). A series of simulation studies uses a macroeconometric model of the UK economy
to assess the CCL package. An important result is “that the energy (and therefore carbon)
saving and energy-efficiency targets would have been met without the CCAs” (Cambridge
Econometrics, 2005, p. 7), which confirms the conclusion drawn above on the lack of target
stringency. Since model simulations of the CCL package give rise to much smaller carbon
savings than official estimates computed for the first compliance period (AEAT, 2004),
Ekins and Etheridge (2006, p. 2079) conclude that “the CCL package as implemented […]
achieved a greater carbon reduction than a no-rebate CCL would have done by itself”. They
attribute this to managers becoming aware of more cost-effective efficiency enhancement
projects as they started to benchmark their energy use. To be sure, the existence of such
an “awareness effect” depends on whether the official carbon savings were real and not
just a consequence of AEAT's (2001) pessimistic BAU scenario. In another simulation study
on the impact of the CCAs on output and employment, a large effect of the CCAs on sectoral
energy demand – averaging a 9.1% reduction in sectoral energy use by 2010 – is built into
the model rather than estimated (Barker et al., 2007). These assessments of the CCL
package highlight two fundamental challenges in policy evaluation, namely (i) to determine
a valid baseline against which to measure the impact of a policy and (ii) to attribute any
measured impact to this policy in a causal fashion. In studies that use simulated
trajectories of energy use as a baseline against which to measure the impact of the CCL
package, the validity of the results critically depends on the counterfactual baseline
being true. In econometric studies based on time series data at the sector level, it is
difficult to discern the effects of the policy from that of unobserved aggregate shocks.15
The present study is the first evaluation of the Climate Change Levy package to use
longitudinal business microdata. We address the baseline problem by comparing changes in
actual firm behavior under two types of policy regimes, thus purging the effect of
aggregate shocks. Moreover, we identify the causal effect of the tax by exploiting
exogenous variation in the eligibility rules for the tax rebate. The next section explains
our research design in detail.

<hs>  Econometric model</hs>
  ~~~~~~~~~~~~~~~~~

Estimation of Eq. (1) recovers the full effect of the CCL if – as previous research has
suggested – CCA targets did not impose binding constraints on firm behavior. If the
converse is true, the estimated α falls short of the true price effect as control plants
choose lower-than-optimal levels of energy so as to comply with their CCA target. Hence,
the estimated parameter α can be regarded as a conservative estimate of the impact of the
CCL. Fig. G.1 in the online appendix illustrates this point.16 In order to estimate α
consistently, one needs to address the issue of non-random selection of plants into the
control group. As we document in Section 4.2 below, CCA plants are, on average, older,
larger and more energy intensive than CCL plants. Clearly, plants using large amounts of
energy receive a larger absolute discount on their CCL liability which gives them a
stronger incentive to join a CCA. In turn, as there are fixed costs of participating in a
CCA, plants with low levels of energy use may find it more profitable not to join.17 This
is illustrated in Fig. G.2a of the online appendix. In principle, selection effects can be
addressed by adding further control variables, but selection might in part be driven by
factors not directly observable to us. For instance, given two plants that initially use
the same amount of energy, the plant with the steeper marginal abatement cost schedule has
a stronger incentive to join the CCA (cf. Fig. G.2b in the online appendix for an
illustration).

<hs>  Instrumental variable</hs>
  ~~~~~~~~~~~~~~~~~~~~~

Eligibility for CCA participation was granted to plants engaged in polluting activities
regulated under the PPC act (listed in Appendix B.1). An eligible plant is comprised of at
least one installation dedicated to the PPC activity, such as a blast furnace or cement
kiln. The discounted rate of the CCL applies to all energy use at this installation.19 We
define the instrumental variable Zi as an indicator variable that equals 0 for all plants
containing at least one eligible installation, and 1 otherwise. The instrument is relevant
because the eligibility of a plant for CCA participation ought to be correlated with its
tax regime. Furthermore, the validity of using ∆Z as an instrument for ∆T in Eq. (2) rests
on the identifying assumption that eligibility is orthogonal to shocks Δϵit that occurred
after 2000. This assumption deserves a careful assessment. For instance, one might worry
that plants could self-select into PCC activities in order to become eligible for the CCA.
Since the entire CCL package was conceived and implemented in a mere two years, and
eligibility rules were established only a year before implementation (in the 2000
Financial Act) it appears unlikely that firms switched technologies in the short run just
because of the CCA discount. Moreover, if PPC regulated and non-regulated plants are
subject to different trends in the outcome variables, the resulting IV estimates will be
biased. In the empirical analysis to follow, we investigate this possibility by looking at
pre-treatment trends but find no evidence of such differences. A visual examination of
time series plots of various outcome variables (shown in Fig. 1 below) suggests no
systematic differences in trends between eligible and non-eligible firms before 2001. The
corresponding statistical test results are reported in panel B of Table 2 and fail to
reject the hypothesis of common trends. Furthermore, our panel dataset allows us to
directly control for differential trends in the outcome regressions. As we discuss in
Section 5.3 below, this does not lead us to reject the hypothesis that outcomes in PPC
firms and non-PPC firms followed a common trend before the introduction of the CCL. Also,
the point estimates of the tax effect hardly change when controlling for pre-trends.
Finally, the exclusion restriction also rules out the possibility that mandatory public
disclosure of PPC pollution in the European Pollution Emissions Register (EPER) had a
direct effect on the outcome variables. While this assumption is untestable, we are not
aware of any evidence that EPER reporting requirements affected firm behavior in the UK.20
Moreover, the fact that pollution emissions in 2001 were published only in 2004 rules out
any direct effects operating through the demand side. It is worth noting that the
exclusive focus on pollution intensity when eligibility was first determined left many
energy intensive industries ineligible for the tax discount. For instance, textile wet
processing was an eligible activity thanks to its high pollution emissions, but not so dry
processing which, although energy intensive, emits no pollution regulated under PPC.
Similarly, both the production and the recycling of glass containers are very energy
intensive processes. However, since only the former is pollution intensive, glass
container recycling was not eligible for CCA participation.21 This institutional ‘glitch’
induces exogenous variation in the probability of treatment even within narrowly defined,
energy intensive industrial sectors.

<hs>  Heterogeneity of the treatment effect</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

So far the treatment effect α was implicitly assumed to be homogeneous across plants. For
the case of heterogeneous responses to treatment, Imbens and Angrist (1994) have shown
that, under certain conditions, the IV estimator identifies the average treatment effect
on “compliers”, i.e. on the subset of the treated for which a change in the instrument
induces a change in treatment status. Although “compliers” need not be representative of
all treated plants, an instrument based on a strict eligibility rule identifies the
average treatment effect on the treated (ATT), simply because non-eligible plants cannot
receive treatment (there are no “always-takers”). This result was first derived by Bloom
(1984) and can be applied to our setting with only minor modifications to the
interpretation. Recall that the treatment we consider is to pay the full tax rate, and
that the instrumental variable indicates whether or not a plant is eligible for an
exemption from treatment. All ineligible plants must pay the full tax rate, so that only
eligible plants are able to escape the treatment (i.e. there are no “never takers”). In
Section D of the online appendix, we show that the IV estimator identifies the average
treatment effect on the non-treated plants (the ATNT), i.e. those that apply for a tax
discount when given the opportunity. We shall refer to this sub-population in a more
intuitive way as the group of “tax concerned” plants. As we explain in more detail below,
we measure eligibility using data from the EPER database. These data cover all facilities
with PPC emissions above certain reporting thresholds, whereas eligibility for a tax
discount was granted regardless of the amount of emissions. In Appendix D we show that
this has no effect on the interpretation of our estimates as long as firms below and above
the reporting threshold do not differ systematically with respect to their treatment
response and their probability of being tax concerned.

<h>DATA</h>
----

The compilation of a dataset suitable for the micro-econometric evaluation of the CCL
required a major effort in terms of data collection, cleaning and matching. The result is
a unique dataset that matches publicly available information on CCA participation and EPER
coverage to production data from two confidential business datasets.

<hs>  Data sources</hs>
  ~~~~~~~~~~~~

The core dataset is the Annual Respondents Database (ARD) which is maintained by the
Office for National Statistics (ONS) and can be accessed by approved researchers through
the UK Data Service's secure access program.22 The ARD is an annual production survey that
covers about 10,000 plants in the manufacturing sector.23 During the sample period, all
plants with 250 employees or more (in some industries: 100 or more) had to report annually
whereas smaller plants were included on a random basis (Barnes and Martin, 2002). The ARD
provides information on the plant's age, number of employees, gross output (revenue),
variable cost, capital stock, materials, and energy expenditures (inclusive of CCL
payments). Detailed information on energy use is taken from the Quarterly Fuels Inquiry
(QFI), a quarterly survey among a panel of about 1000 manufacturing plants managed by the
ONS on behalf of DTI. The survey collects data on expenditures and quantities for all
relevant fuel types, including medium fuel oil, heavy fuel oil, gas oil, liquefied
petroleum gas (LPG), coal (graded, smalls), hard coke, natural gas, and electricity. We
have data for the period from 1993 to 2004. The majority (83%) of the observations in the
QFI can be matched to the ARD without difficulty because both surveys use the same
underlying government business register IDBR as their sampling frame. However, due to
random sampling in the ARD we do not have ARD data for all QFI plants.24 We gathered
information on CCA participation from both the DEFRA and HM Revenue and Customs (HMRC)
websites. Lists of facilities in the original sector agreements were downloaded from
DEFRA's website. The agreements stipulate the certification periods and the sector targets
along with the details on the calculation of the units of energy used and carbon
emissions. They also contain a list of all facilities initially covered by the CCAs. Seven
agreements lack sufficient information on the facilities covered by the CCA and thus had
to be excluded from the analysis.25 The HMRC website provides, sector by sector, the list
of facilities that have joined the CCA along with the date of publication.26 The lists are
regularly updated and facilities that have resigned from the CCA are removed. We merged
the DEFRA and HMRC lists to obtain a complete list of facilities that pay the reduced rate
of the CCL. We match this information to the ARD and QFI by combining information on a
plant's postcode and the UK Company Register Number (CRN). To construct the instrumental
variable, we downloaded publicly available data from the European Pollution Emissions
Register (EPER) which covers all European facilities regulated under the IPPC directive
whose emissions exceed the reporting thresholds. The 2001 EPER file contains reporting
thresholds and pollution discharges into air and water for 50 pollutants and covers 2397
facilities in 56 sectors of activity in the UK. We construct the instrumental variable
NEPER as a dummy variable that equals one if a facility is not on the EPER list, i.e. it
does not report emissions of any of the pollutants regulated under PPC legislation. A
value of zero is assigned otherwise. Just like the treatment variable T, this variable is
zero for all plants before 2001 and does not vary between 2001 and 2004. To match EPER
facilities to plants in our dataset we use the same algorithm that we used for matching
CCA participation data.

<hs>  Descriptive statistics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

Our regression sample comprises 6886 and 1079 plants in the ARD and QFI datasets,
respectively.27 Table G.1 in the online appendix reports descriptive statistics. We
calculate energy intensity as the share of energy expenditures in either gross output or
variable costs (the sum of expenditures on materials, energy and wages), finding a
substantial amount of dispersion between plants. For example, the energy expenditure share
in gross output of a plant at the 90th percentile is seven times larger than that of a
plant at the 10th percentile. We report both quantities consumed and expenditures paid for
the fuel variables, after aggregating up some of the variables available in the QFI to
obtain the categories liquid fuels (oil, petrol, and LPG), solid fuels (coal and coke) and
natural gas (firm contract, interruptible contract, tariff). Moreover, we compute the
share of natural gas in the consumption of both gas and electricity, and total CO2
emissions (in thousands of tonnes) on the basis of the fuel mix. The regression sample
starts in 1999, because this is the first year for which energy expenditure data are
available in the ARD, and covers the first two target periods that lasted from 2001 until
2004. This window of analysis avoids possible complications due to (i) an overlap with the
EU ETS which affected approximately 500 CCA plants from 2005 onwards, (ii) adjustments of
CCA targets for the third compliance period, and (iii) new entry of sectors in 2006
following changes in the eligibility rules. Table 2 displays the means of the main
variables in the pre-treatment year 2000 (panel A) and the differences between year 2000
and 1999 (panel B), broken down by treatment and eligibility status.28 The treatment
variable CCL takes a value of one if a plant pays the full tax rate and a value of zero if
the plant participates in a CCA. Panel A shows that participation in CCAs is not random:
CCA plants are, on average, older, larger and more energy intensive. For most of these
plant characteristics, a t-test of equal group means for CCL and CCA plants rejects at the
1% significance level. Given this strong correlation between treatment status and
observable plant characteristics, we cannot rule out that unobservable plant
characteristics also influence selection. We address selection in levels by differencing
out fixed unobserved plant characteristics in Eq. (2). To mitigate bias from selection on
changes in the outcome variables, we instrument the difference regression using
eligibility which is presumably exogenous to innovations in the outcome variables. This
assumption is more credible if we find that eligible and non-eligible plants do not follow
systematically different trends in terms of the outcome variables ahead of the treatment.
We examine this in Fig. 1 by plotting average changes in the main outcome variables with
respect to the year 2000, both for eligible and non-eligible plants, as well as by
treatment status.29 This shows that trends were closely aligned when treatment was
imminent. More formally, panel B of Table 2 reports the pre-treatment growth rates by
treatment and eligibility status, along with the results of a t-test for group equality.
The test never rejects at the 5% level, suggesting that differential pre-trends in outcome
variables were not important. This mitigates concerns about changes in the outcome
variables being confounded with unobserved attributes of eligible firms. Finally,
selection bias might also arise if attrition rates are systematically related to treatment
status. We investigate this in Section 6.3 below, finding no significant impact of the CCL
on plant exit relative to CCA plants.

<hs>  Determinants of CCL status</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~

Table 3 reports the results from various regressions of CCL status on NEPER and other
plant characteristics. Each regression is run in both the ARD and the QFI samples. Columns
1 and 4 report the marginal effects from a probit regression of CCL on NEPER in the cross
section for the year 2001. The coefficients imply that a value of NEPER = 1 increases a
plant's chances of paying the tax in full by 28.4% in the ARD sample and by 44% in the QFI
sample. The results from the first-stage regression underlying the IV estimation of Eq.
(2) in first differences are reported in columns 2 and 5. They corroborate that there is a
robust positive and statistically significant relationship between the treatment variable
and the instrument. Columns 3 and 6 display the results from a probit regression of CCL
status in 2001 on various plant level controls evaluated at their 2000 levels. The
coefficient estimates show that the simple correlations between CCL status and plant
characteristics we found in Table 2 persist after controlling for sectoral differences. In
particular, plants that were larger in terms of their capital and energy inputs prior to
treatment were more likely to participate in a CCA. The coefficients on energy and gross
output suggest that the same is true of more energy intensive plants. In Section B.2 of
the online appendix we present further evidence pointing to size and energy intensity as
the main determinants for take up among eligible plants. This is consistent with the
notion that the 80% discount on the energy tax rate would allow only large and energy-
intensive plants to accumulate enough tax savings to cover the fixed costs of CCA
participation.

<hs>  Treatment effect of the CCL</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~

The first two rows in panel A of Table 4 report the results for energy intensity measured
as the share of energy expenditures in either gross output and variable costs,
respectively. We find that the CCL caused plants to decrease their energy intensity
relative to CCA plants. The point estimates from the IV regressions are − 0.181 for the
former measure and − 0.211 for the latter. The effects are both economically and
statistically significant. The importance of controlling for selection is evident from the
sizable differences between the OLS and IV estimates. In particular, OLS estimation leads
to an upward bias when estimating the effect of the CCL on the growth in energy intensity.
This is because the OLS estimator does not correct for the self-selection of energy
intensive plants into the low-tax regime, which we found in Table 3 above. As we show in
Section 6.1 below, this type of plant responded more strongly to the CCL, causing bias
towards zero in the OLS estimates. In rows 3 and 4, we break down the effect on energy
intensity by looking at its components. The IV point estimates of − 0.095 for energy
expenditure and 0.086 for gross output suggest that CCL plants both reduced energy and
increased gross output so as to achieve the reductions in energy intensity reported in row
1. However, the point estimates are imprecise and lack statistical significance at
conventional levels. This reflects the fact that both variables lump together prices and
quantities, which are likely to move in opposing directions and thus attenuate the effect
of higher energy prices.30 Furthermore, we obtain a positive but not statistically
significant point estimate for employment of 0.082. We derive an estimate of the CCL
impact on TFP from an augmented Eq. (1) which includes the production factors capital,
labor, materials, and energy. This amounts to estimating a production function where the
treatment variable captures the impact of the CCL on otherwise unexplained differences in
TFP.31 The coefficients reported in row 6 are positive but small in magnitude and lack
statistical significance. We thus cannot reject the hypothesis that the CCL had no effect
on plant-level TFP. The evidence in panel A clearly shows that the CCL led to substantial
reductions in plant-level energy intensity compared to the CCA. While the other
coefficients are estimated less precisely, the point estimates are consistent with firms
substituting labor for energy and increasing output prices in response to the energy price
increase. In Appendix E we show that all the qualitative results in Panel A – including
the stronger response of energy intensity than energy expenditures – can be generated by a
simple equilibrium model with neo-classical production functions that exhibit a
sufficiently large degree of substitutability between labor and energy. The CCL package
was not part of any harmonized carbon tax scheme for Europe but a unilateral policy
measure. As such, it may have had a detrimental effect on the competitiveness of UK
industry. On the basis of the positive but insignificant point estimates we obtain for
employment and gross output, however, we cannot reject the hypothesis that the CCL did not
cause firms to shed jobs or lose revenue relative to CCA firms. While it seems plausible
that the CCL lowered profits we cannot estimate this effect directly for lack of pertinent
data. However, if profit losses were substantial they might have induced firms to shut
down some plants. We examine this possibility in Section 6.3 below. From a climate-policy
perspective, it is important to know whether reductions in energy expenditures in CCL
plants actually occurred, whether they corresponded to reductions in energy consumption
and whether they lowered carbon emissions. For example, instead of consuming less of all
fuel types CCL plants might substitute towards fuels that are cheaper but also more
polluting, such as coal. More detailed information on energy use is needed to address this
issue, as the energy expenditures variable lumps together changes in the tax-inclusive
price and quantity of energy, as well as the effects of substitution between different
fuel types. Panel B of Table 4 reports results from regressions using quantity changes in
energy consumption by fuel type which are available in the QFI sample. Although this
sample is smaller than the ARD sample, we find economically and statistically significant
evidence that the CCL caused plants to decrease their electricity use by 22.6%. For
natural gas, solid fuels, and solid fuels as a share of total kWh consumed we obtain
positive point estimates of the treatment effect.32 However, the coefficients are not
estimated with enough precision to support conclusions about interfuel substitution. The
significant decrease in electricity consumption among CCL plants translates into a
decrease in carbon dioxide emissions ceteris paribus, but this could be offset by an
increase in the consumption of other fuel types. The last row of Table 4 shows the impact
of the CCL on total CO2 emissions, calculated as the sum of emissions across fuel types.
The CCL is associated with a significant decrease in total CO2 emissions of 7.3% in the
OLS regression. The point estimate increases slightly when going from OLS to IV, yet
statistical significance is lost. We conjecture that this is due to the noisy estimates of
the tax response for fuels other than electricity. In the absence of a larger sample that
would enable us to estimate this effect with more precision, there are two possible ways
of quantifying the effect of the CCL on carbon emissions. On the one hand, one can choose
to disregard statistically insignificant coefficients altogether and conclude that the
unchecked decrease in electricity consumption translates into a decrease in CO2 emissions
of equal magnitude. On the other hand, a more cautious interpretation of the results is to
use the point estimate of − 0.084 from the IV estimation which accounts for the
possibility that some CCL plants switched into dirtier fuels such as coal. We thus
conclude that the CCL – though not designed as a pure carbon tax – caused plants paying
the full rate to reduce CO2 emissions by between 8.4% and 22.6% compared to plants that
paid the reduced rate. In further regressions, reported in Section F of the online
appendix, we interact the treatment indicator with year dummies so as to recover the time
profile of the treatment response following the introduction of the CCL. This can reveal
possible time delay in plants' responses to the treatment, or whether the treatment effect
dies off after a while. We find that the tax has the largest effect on the ARD outcome
variables in the first two years of treatment. While the negative impact of the CCL on
electricity use is statistically significant from 2002 onwards, the point estimates for
natural gas and coal are usually not statistically significant at the 5% level.33

     <hss>Balanced sample</hss>

        Our sample is an unbalanced panel for a number of reasons: random sampling of
        smaller plants in the ARD, plant births and deaths, and missing responses from
        some plants in some years. As the set of plants in the sample changes slightly
        from year to year, the time profile of the treatment effect might reflect – at
        least in part – the changes in sample composition rather than the dynamic response
        to the CCL. Another potential problem with the unbalanced panel is that the
        results could be dominated by potentially more extreme responses of exitors. To
        address these concerns, we estimate the model with time interactions in a subset
        of “stayer” plants with observations in all years after 1999. The results are
        summarized in Tables G.4–G.6 in the online appendix. Since the sample size drops
        by about half in both samples, some of the estimated treatment effects lose
        statistical significance. However, the qualitative findings remain similar to the
        ones estimated on the full sample.

     <hss>Controlling for pre-treatment trends</hss>

        Our identification strategy relies on the (untestable) assumption that differences
        between eligible and non-eligible plants are not systematically related to changes
        in outcome variables over the treatment period. In Section 4.2, we have shown that
        pre-treatment trends did not differ across these groups in a statistically
        significant way, meaning that our estimates are unlikely to confound the impact of
        the treatment with pre-existing differences. To corroborate this, we include a
        time-invariant eligibility dummy in Eq. (2) so as to directly control for
        unobserved trends in the outcome variables, separately by eligibility status. 34
        Tables G.7 and G.8 in the online appendix show that this yields qualitatively
        similar results, albeit less statistically significant ones in later years. Since
        the coefficients on the eligibility dummy are statistically insignificant for all
        outcome variables except solid fuels, we do not include them in our preferred
        specification.

     <hss>Common support regression</hss>

        Despite our IV strategy there might be concern that results are driven by a
        fundamental heterogeneity between treated (eligible) and non-treated (non-
        eligible) plants. Therefore, as a robustness test we restrict the control group to
        a common support which is identified by the predicted probability of a plant in
        the control group to receive treatment.35 We construct this common support sample
        by dropping plants that do not belong to the central 80% of the propensity score
        distribution, while also balancing the covariates between the treatment and the
        control group.36 The results obtained for the common support sample are reported
        in Table G.9 of the online appendix. For the ARD variables in panel A this leads
        to slightly larger point estimates, suggesting that heterogeneity within the
        treated group is not a major problem. In the smaller QFI dataset, about half of
        the sample needs to be dropped, but this entails no qualitative change to the
        results.

<hs>  The impact of the CCL in different subsamples</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our discussion so far has focused on the average effect of the CCL on non-treated plants.
It is useful to know how this effect varies across plants with certain characteristics.
For example, the tax impact may differ from the ATNT in industries that are very energy
intensive because the levy imposes a higher cost burden on these industries. Moreover, as
the political cost of job losses is high, policy-makers might be interested in the tax
impact on small firms which are responsible for the bulk of total employment. Finally, the
impact of the CCL on competitiveness may be particularly high for firms in sectors with
high import penetration, as foreign competition prevents them from passing compliance cost
on to their customers through higher output prices. To shed light on this, we estimate the
impact of the CCL separately: (i) for plants with more vs. less than 250 employees, (ii)
for plants with high vs. low energy intensity and (iii) for plants with high vs. low trade
intensity.37 The first two columns of Table 5 report the IV coefficients for the split by
energy intensity, defined as the share of energy expenditures in gross output. Results for
the low- and high-intensity groups are reported in the odd and even-numbered columns,
respectively. The IV point estimates for energy intensity and energy expenditures indicate
that the average effects reported in Table 4 are due to a strong response by plants in
energy intensive sectors. The point estimates in this group are − 0.195 for energy
intensity and − 0.154 for energy expenditures, both are statistically significant at 5%.
In contrast, the point estimates for the low-intensity group lack statistical
significance. The point estimates for electricity consumption are similar in magnitude
across groups but lack statistical significance in the low-intensity group. In columns 3
and 4 of Table 5 we split the sample according to the trade intensity in 4-digit NACE
sectors, which is computed as the value of imports and exports to non-EU countries over
the total market size within the EU27.38 This measure has been used by the EU Commission
to gauge the competitiveness impact of the EU ETS on manufacturing firms. To the extent
that trade intensity measures the degree of competition from non-regulated countries, it
picks up the (lack of) ability of firms to pass on the cost of the CCL to their customers.
The point estimates for the ARD variables obtained in the trade intensive group closely
follow those obtained in the full ARD sample. In contrast, the impact on energy intensity
is not statistically significant in the low-intensity group. We do not find any
significant impact on employment in either of the two groups. This gives rise to two
interpretations: first, that trade intensity might not be a good criterion for identifying
adverse effects on competitiveness; or second, that the hypothesis which states that there
are no such effects should not be rejected. The last two columns of Table 5 report the
results for the employment split. While the point estimates for energy expenditures in
small plants and electricity use in large plants are negative and statistically
significant at the 10% level, no clear pattern emerges from this comparison across size
groups.

<hs>  Aggregate effects of a carbon tax</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

While the micro-level approach allows for better identification of the causal impacts of
the tax, from a policy point-of-view the aggregate implications of the tax matter. In this
section, we compute the effect of a counterfactual carbon tax similar to the CCL but
without the reduced tax rate. This exercise allows us to compare our results to studies
assessing the impact of energy price changes on fuel consumption at the aggregate level.
Both numbers are at the upper end of elasticity estimates obtained in comparable studies.
For example, Bjorner and Jensen (2002) estimate the energy price elasticity at 1.37 in the
pooled cross-section and 0.50 in a fixed-effects specification.41 The reader should bear
in mind, however, that we recover an estimate of a tax-induced price elasticity. Davis and
Kilian (2011) argue that this is structurally different from elasticity estimates based on
other kinds of price variation because taxes may be perceived as more persistent and hence
induce larger behavioral changes. They also point to a possible additional effect of media
coverage that accompanies the introduction of such taxes. Since the CCL was promoted as
the UK's flagship regulation for mitigating climate change, there was ample scope for such
an effect of the CCL, and our comparatively large estimates do not speak against this
possibility.

<hs>  The CCL and plant exit</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

The analysis so far has focused on how paying the full rate of the CCL affects various
outcome variables in surviving plants. Rather than adjusting energy use and production at
the intensive margin, there is a concern that firms might respond to the CCL by closing
down plants altogether or by re-locating to non-regulated countries (“pollution havens”).
After all, the substantial tax rebates granted under the CCA are intended to prevent such
extensive-margin adjustments by energy intensive firms.42 This allows for fixed
differences in the exit propensity between small and large plants and, since employment
size and treatment status are strongly correlated (see Table 2), SMALL may also, to a
large extent, control for fixed heterogeneity between treatment and control groups.
Moreover, we use the interaction of SMALLi with a post-treatment dummy I{t > 2000} to
instrument for CCLit. The idea behind this is (i) to use the fact that size influenced the
decision to participate in a CCA and (ii) to rely on variation in size prior to our sample
period so as to preserve the exogeneity of the instrument. The estimated coefficient α has
the interpretation of a local average treatment effect (LATE). Since all the information
needed to estimate Eq. (6) is available from the IDBR, we implement these regressions at
the local unit level (see footnote 23 above). Table 6 reports the results from probit and
IV probit models, along with the corresponding reduced-form (RF) and first-stage (FS)
results. In each of the exit regressions, the coefficient on SMALL is positive and
significant, confirming the already well-documented empirical regularity that smaller
firms are more likely to exit. The simple probit model yields a positive and significant
coefficient estimate on CCL which implies a 5.9% increase of the exit probability at the
average CCL plant. Notice that this effect is not necessarily causal. In fact, the
positive coefficient is consistent with a reverse-causality explanation according to
which, plants that anticipate to exit in the near future do not sign a CCA because the tax
savings this generates over the remaining lifetime of the plant do not cover the fixed
costs of certification to be paid upfront. Once we instrument for CCL status, the point
estimate becomes statistically insignificant, as foreshadowed by the insignificant
coefficient estimate on the instrument obtained in the reduced form. The first-stage
regression coefficients show that our instrument is strongly correlated with CCL status.
In sum, we find no evidence that the CCL had an impact on plant exit decisions. This
finding is robust to the inclusion of industry controls and to splitting the sample by
either energy or trade intensity as in Section 6.1 above.44 Our analysis has focused on
exit decisions at the local unit level whereas the bulk of the variables used in Section 5
are only available at a slightly higher level of aggregation (the ‘reporting unit’ or
‘plant’). Since employment (and only employment) is available at both levels of
aggregation, we re-estimate a version of Eq. (2) using employment data at the local unit
level in order to verify that the results obtained at the reporting unit level are robust.
Table 7 reports estimates of the CCL impact on employment in the full sample and when the
sample is split according to energy and trade intensities, or size (defined as above at
the reporting unit level). Our preferred specification includes a trend coefficient for
the treatment group (NEPER × year diff) because we find it to be statistically significant
for the high trade intensity group.45 As before, we do not find evidence of a detrimental
effect of the CCL on employment, regardless of which way the data are cut.

<h>CONCLUSION</h>
----------

There is a growing consensus that climate policy should aim to regulate GHG emissions
efficiently across a broad range of economic sectors. While curbing industrial emissions
must be an integral part of any such policy, there is surprisingly little empirical
evidence on the impacts of large-scale regulations of industrial GHG emissions — let alone
using market-based instruments. In this paper we have provided the first micro-econometric
evaluation of a carbon tax on the manufacturing sector. Unlike simulation-based
evaluations, our approach does not require making assumptions about counterfactual –
“baseline” – trends in the outcome variable of interest. Instead, we compare changes in
outcomes both over time and between plants that were subject to different tax rates. The
“baseline” is hence given by the contemporaneous outcomes of plants that faced lower tax
rates by virtue of being in a CCA. Our estimates of the impact of the CCL are thus purged
of confounding factors that affect plant performance at the level of the economy, the
region and the sector. Since we also control for self-selection into CCAs by exploiting
exogenous variation in CCA eligibility rules, we interpret our estimates as the causal
effect of the CCL on plant outcomes. We find robust evidence that the price incentive
provided by the CCL led to larger reductions in energy intensity and electricity use than
the energy efficiency or consumption targets agreed under the CCA. The tax discount
granted to CCA plants has been justified as a means of preventing energy intensive firms
from losing competitiveness in international product markets due to the unilateral
implementation of the tax and to the lack of international harmonization. Although this
has been widely argued, we find no discernible impact on employment, gross output or
productivity across groups, and we cannot reject the hypothesis that the CCL had no impact
on plant exit. Our results show that the introduction of a moderate tax on energy
encourages electricity conservation and helps to reduce energy intensity in the
manufacturing sector. This is in contrast to previous research that attributed substantial
carbon savings to the CCA scheme on the basis of comparisons with counterfactual baseline
emissions (Ekins and Etheridge, 2006; Barker et al., 2007; AEAT, 2004).46 While our
research design arguably produces a more credible estimate of the effect of the CCL, it is
clear that this effect is additional to any effect the CCA targets may have had on firm
behavior. Our study constitutes a first step towards building an evidence base that
informs policymakers about the impacts of climate change policies on industry. As more
such policies are being implemented across countries, and as business microdata are
becoming more abundant and easier to access, we expect that researchers will exploit the
variation in policies and institutional settings to make important contributions to this
evidence base. In the context of climate change policy in the UK, there are several issues
that deserve attention in future research. First, it seems important to gain a better
understanding of how plants achieved the substantial reductions in energy use that we
measure. This will require gathering more qualitative information on the key drivers of
energy conservation — be they technical, economic or managerial. This information could
lead to the design of more sophisticated policy instruments. From a political economy
point-of-view, an analysis of the bargaining over CCA targets and of compliance behavior
of individual CCA facilities will provide valuable insights regarding the design of
negotiated agreements. Finally, given the long-term nature of climate change, an important
open question is whether a moderate energy tax such as the CCL can stimulate much-needed
innovation to bring about substantial carbon reductions in the future.


<h>REFERENCES</h>
----------

  [7] Terry Barker, Paul Ekins, Tim Foxon. Macroeconomic effects of efficiency policies for energy-intensive industries: The case of the UK Climate Change Agreements, 2000-2010. doi:10.1016/j.eneco.2006.12.008
  [9] Thomas Bue Bjørner, Henrik Holm Jensen. Energy taxes, voluntary agreements and investment subsidies-A micro-panel analysis of the effect on Danish industrial companies' energy demand. doi:10.1016/S0928-7655(01)00049-5
  [10] Howard S. Bloom. Accounting for no-shows in experimental evaluation designs. doi:10.1177/0193841X8400800205
  [12] Lucas W. Davis, Lutz Kilian. Estimating the effect of a gasoline tax on carbon emissions. doi:10.1002/jae.1156
  [15] Paul Ekins, Ben Etheridge. The environmental and economic impacts of the UK climate change agreements. doi:10.1016/j.enpol.2005.01.008
  [21] Scott R. Milliman, Raymond Prince. Firm incentives to promote technological change in pollution control. doi:10.1016/0095-0696(89)90019-3
  [22] W. David Montgomery. Markets in licenses and efficient pollution control programs. doi:10.1016/0022-0531(72)90049-X
  [25] S. Pacala, R. Socolow. Stabilization wedges: Solving the climate problem for the next 50 years with current technologies. doi:10.1126/science.1100103
  [26] David Pearce. The political economy of an energy tax: The United Kingdom's Climate Change Levy. doi:10.1016/j.eneco.2005.10.001
  [27] Stephen Smith, Joseph Swierzbinski. Assessing the performance of the UK Emissions Trading Scheme. doi:10.1007/s10640-007-9108-5
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<ART>The importance of peers for compliance with norms of fair sharing
=================================================================

Authors: Simon Gächter, Leonie Gerhards, Daniele Nosenzo
DOI: 10.1016/j.euroecorev.2017.06.001
Year: 2017  |  Pages: 72-86
ASJC codes: 2002, 2003
Keywords: Dictator game, Experiments, Fair sharing, Framing, Norm compliance, Peer effects, Social norms

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

A burgeoning literature in economics has started examining the role of social norms in explaining economic behavior. Surprisingly, the vast majority of this literature has studied social norms in asocial decision settings, where individuals are observed to act in isolation from each other. In this paper we use a large-scale dictator game experiment (N = 850) to show that “peers” can have a profound influence on individuals’ perceptions of norms of fair sharing, which we elicit in an incentive compatible way. However, in contrast to these strong peer effects in social norms of fair sharing, we find limited evidence of the influence of norms and peers on actual sharing behavior. We discuss how these results can be explained by heterogeneity in normative views as well as in willingness to comply with norms.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

We study the driving forces underlying one of the fundamental principles of human social
behavior: fair sharing. While earlier explanations have focused on the role of other-
regarding preferences and preferences for equality (see, e.g., Camerer, 2003, Chap. 2), we
investigate a more recent account of fair sharing that relies on the concept of norm
compliance: many people have an intrinsic preference to conform to what is collectively
perceived as “socially appropriate” and are willing to sacrifice material gain in order to
comply with such norms.1 In fact, social norms are thought to drive behavior in a variety
of social contexts (e.g., Elster, 1989; Bicchieri, 2006; López-Pérez, 2008; Krupka and
Weber, 2013). A number of recent experimental studies use a norm compliance framework to
explain behavior across several settings, including dictator games (Krupka and Weber,
2013; Krupka et al., 2017; Kimbrough and Vostroknutov, 2016), third-party allocator games
(Barr et al., 2015), gift-exchange games (Gächter et al., 2013), oligopoly games (Krupka
et al., 2017), public good, trust and ultimatum games (Kimbrough and Vostroknutov, 2016).
However, nearly all of these studies of social norms focus on tightly controlled, but
surprisingly asocial decision environments, where individuals face neutral and abstract
decision situations, under full anonymity, and in complete isolation from other decision-
makers. While the use of contextually sterile decision environments is one of the
hallmarks of experimental control, we also notice that contextual variables – from the
framing of the decision task to the presence and behavior of other decision-makers in the
decision setting – play a crucial role in nearly every conceptual account of social norms.
Minimal variations in the context can profoundly change individuals’ perception of the
nature of the decision situation and the underlying norms of conduct (Bicchieri, 2006).
This highlights the importance of studying the interaction between contextual variables
and norm compliance. In this paper we take a step in this direction by systematically
studying the influence on norm compliance in fair sharing of one specific contextual
variable: the presence of “peers”, i.e. other decision-makers, in the decision setting
faced by an individual. We believe that understanding the influence of peers on individual
decision-making is important for a number of reasons. First, information about peer
behavior is typically available in many natural social settings, where individuals do not
act in social isolation. On the contrary, people often have the opportunity to interact
with others and observe their choices before making a decision. Thus, studying the
influence of peers on individual decision-making is inherently relevant for understanding
the general dynamics of human social interactions. Second, the study of peer influence is
of theoretical interest because peers are an important determinant of norm-driven behavior
in most conceptual accounts of norm compliance across the social sciences. For instance,
in economics, Sugden (1998) argues that observing instances of norm-compliance or norm-
breaking can reinforce or weaken the expectations that the norm ought to be followed. In
social psychology, Cialdini et al. (1990) contend that the behavior of peers exerts
normative influence on individual behavior by shaping what individuals perceive as typical
or normal behavior in a given situation (the “descriptive norm”). In philosophy, Bicchieri
(2006) proposes that whether or not a norm will be followed depends partly on “normative
expectations” (whether the individual expects that sufficiently many others expect him or
her to comply), and partly on “empirical expectations” (whether the individual expects
that sufficiently many others will comply). Sociologists Lindenberg and Steg (2013) argue
that the behavior of others can shift the weights that individuals place on the normative-
goal (following social norms) relative to the more self-centered hedonic and gain goals
(need satisfaction and resource accumulation). Despite the large theoretical literature on
the importance of peers for norm-driven behavior, the empirical evidence is scant. In many
of the settings where peer effects have been documented empirically (e.g., Keizer et al.,
2008; Shang and Croson, 2009; Bicchieri and Xiao, 2009; Krupka and Weber, 2009; Gächter et
al., 2012; Falk et al., 2013; Thöni and Gächter, 2015), other behavioral forces may
explain the correlations between individuals’ and peers’ actions observed in the
experiments.2 Even in settings where the observed data patterns are difficult to reconcile
with alternative explanations (e.g. McDonald et al., 2013) and results are strongly
suggestive that the presence of peers affects norms, the lack of direct data on how peers
affect normative considerations makes it difficult to identify whether the observed impact
of peers’ actions on behavior is mediated by corresponding shifts in the normative
evaluation of actions. In this paper we present a new set of dictator game experiments
that measure the influence of peers on both actual sharing and norms of sharing using the
incentive-compatible norm-elicitation task by Krupka and Weber (2013).3 Our experiments
set us apart from the existing literature on peer effects mentioned above, in that we are
able to explicitly identify the linkages between peers’ actions, normative views, and
individual sharing behavior. In this aspect our paper is related to Gächter et al. (2013),
who, however, study peer effects in norms and behavior in a gift exchange game. They find
that peer effects in norms do not explain the observed peer effects in actual gift
exchange. While these results cast some doubt on the importance of norms for peer effects,
it would be premature to base judgment on the importance of norm following solely on the
study of one specific decision setting and one specific social norm. It is indeed unclear
whether the results from the gift exchange game may also extend to other settings and
norms, as it may be the case that the influence of peer behavior is more decisive for
norms of fair sharing than for reciprocal gift exchange. Moreover, all the experiments
reported in Gächter et al. (2013) are based on gift exchange games where the decision-
makers observe the decisions of a peer before making their own choices. In this sense, it
is not obvious that their experiments allow assessing the causal impact that the presence
of peers may have on norms and behavior, because their study lacks a treatment without
peers. In this paper, we study settings where the decision-maker is exposed to the
influence of a peer as well as settings where the decision-maker acts in isolation from
peers. This allows us to examine the causal influence that peers have on norms and
behavior. Specifically, in our Peer treatment subjects play a sequential three-person
dictator game, where two dictators can transfer money to one recipient. The dictators move
sequentially and thus the second dictator can observe the transfer made by the first
dictator (the “peer”) before making her own transfer decision. In contrast, our NoPeer
treatment is based on a two-person dictator game where there is no peer and her role is
replaced with Nature: in this game, Nature moves first and randomly determines an
endowment for the recipient; the dictator observes this endowment and then transfers money
to the recipient. The crucial difference between the two treatments is thus that, while in
the Peer treatment the recipient's wealth (prior to the dictator's transfer) is determined
by a peer, in the NoPeer treatment it is determined by chance and there is no decision-
maker other than the dictator present in the decision context. Furthermore, to
systematically investigate the extent to which the influence of peers on normative
considerations and behavior depends on the nature of the underlying norms, our study
examines two payoff-equivalent, but differently framed, versions of the dictator game. In
one version the dictator can give money to another player, while in the other version the
dictator can also take money from the other player. Krupka and Weber (2013) have used
similar versions of the dictator game to measure the influence of norms on dictator's
behavior.4 They have shown that these “give” and “take” versions of the dictator game
produce stark differences in the amounts of money that dictators share with recipients.
Moreover, they explain these differences by the fact that the norm that governs behavior
in the “give” version of the game is substantially different from the norm that applies to
the “take” game. Hence, we use give/take framing to study the extent to which the
influence of peers depends on the nature of the norm (norm of giving vs. norm of taking).
To summarize, our study is based on four treatments, using a 2 × 2 factorial design where
we vary the frame of the game (Give vs. Take) and whether a peer is present or absent
(Peer vs. NoPeer). For each treatment, we conduct two types of experiments, a norm-
elicitation experiment and a behavioral experiment. In the norm-elicitation experiment, we
follow Krupka and Weber (2013) and measure in an incentive compatible way the extent to
which the peer's behavior affects the perception of what constitutes socially appropriate
behavior. In the behavioral experiment, we check how these variations in perceptions of
social appropriateness translate into actual decisions. A total of 850 subjects
participated in our experiments. Our norm-elicitation experiments reveal that the presence
of peers has a systematic and strong influence on the perceptions of social
appropriateness. In the Peer treatment, ungenerous monetary transfers to the recipient are
viewed as relatively more appropriate when the peer is also ungenerous towards the
recipient. However, when the same levels of recipient's wealth have been determined by
chance (NoPeer treatment), the relation between recipient's wealth and appropriateness is
reversed: ungenerous transfers are viewed as relatively more appropriate when the
recipient is wealthier (i.e. when the recipient has randomly received a larger endowment).
Interestingly, we also find that the strength of these effects varies considerably across
our two versions of the dictator game. The norm that governs behavior in the Take game is
much more stable and resilient to peer influence than the norm in the Give game. Based on
the results of the norm-elicitation experiment, we should expect to observe systematic
differences in the influence of peers’ actions (and hence recipient's wealth) on
dictator's actual behavior across our experimental conditions. In particular, we should
expect a positive relation between dictator transfers and recipient wealth in the Peer
treatment, while a negative relation should emerge in the NoPeer treatment. Moreover,
these treatment differences should be more pronounced in the Give than in the Take game.
The results of our behavioral experiments are only partially in line with these
expectations. While we observe that dictators in the NoPeer treatment significantly reduce
their transfers when the recipient possesses larger endowments, there is, on average, no
relation between dictator and peer transfers in the Peer treatment. Moreover, we do not
detect any differences in the magnitude of these effects between the Give and Take
conditions. The absence of a peer effect in the Peer treatment is consistent with the
findings reported by Panchanathan et al. (2013). They also conduct a three-person dictator
game experiment where two dictators decide sequentially how much to give to a recipient.
They find that, on average, the amount given by the first dictator does not affect the
second dictator's giving. At the individual level, they observe substantial heterogeneity
in the second dictator's responses: while some dictators increase their giving in the
amount given by the peer, others give less when the peer gives more, and others do not
vary their giving with the peer's giving. We observe similar heterogeneity in our
experiment. This suggests that a potential explanation for the limited support of the norm
compliance model in our experiments may lie in the existence of conflicting views about
what constitutes a norm in our setting. In Section 5 we examine this possibility in detail
and show that there is considerable heterogeneity in the extent to which participants
agree on what a norm is in our experiments as well as in the extent to which they are
prepared to comply with it.

<h>EXPERIMENTAL DESIGN AND PROCEDURES</h>
----------------------------------

All our treatments are based on dictator game experiments. The Peer treatment is based on
a three-person sequential dictator game where two dictators (D1 and D2) are matched with
one recipient (R). Dictators move sequentially: D1 moves first and chooses a monetary
transfer for the recipient; D2 observes the transfer chosen by D1 and then chooses a
transfer. In the Give version of the game, D1 and D2 receive an initial endowment of £12
each, while the recipient is endowed with £0. Each dictator can then transfer an amount
gi∈{D1, D2} ∈ {£0, £1, £2, £3, £4} from her endowment to the recipient. Monetary payoffs
are computed as πi = £12 – gi for a dictator, and πR = £0 + gD1 + gD2 for the recipient.7
We study how D2’s behavior is affected by information about their peer's (D1) behavior, by
comparing choices made in the Peer treatment with choices made in the NoPeer treatment,
where the role of D1 is replaced with Nature. Thus, the NoPeer treatment is based on a
two-person dictator game, where one dictator is matched with one recipient. In the Give
version of the game, the dictator receives an endowment of £12 while the recipient's
endowment, E = {£0, £1, £2, £3, £4}, is randomly determined by Nature. After observing the
value of the recipient's endowment, the dictator transfers an amount g ∈ {£0, £1, £2, £3,
£4} to the recipient. Payoffs are computed as πD = £12 – g for the dictator, and πR = E +
g for the recipient. Note that in both treatments we observe decisions by dictators facing
the same five possible situations, each corresponding to a different level of initial
wealth of the recipient (£0, £1, £2, £3, or £4). The difference between the two treatments
is that in the Peer treatment the recipient's wealth (prior to the dictator's transfer) is
determined by the donation of another dictator, whereas in NoPeer the peer is absent and
the recipient's wealth is determined at random.8 The corresponding Take versions of the
games are analogously defined, except that the initial distributions of endowments differ
relative to the Give version. In the Peer/Take game, D1 and D2 are endowed with £9 each,
while the recipient is endowed with £6. Each dictator can give/take an amount ti∈{D1, D2}
∈ {−£3, −£2, −£1, £0, £1} to/from the recipient. Payoffs are computed as πi = £9 – ti for
a dictator, and πR = £6 + tD1 + tD2 for the recipient. Analogously, in the NoPeer/Take
game the dictator is endowed with £9, while the recipient's endowment is randomly
determined from the set E = {£3, £4, £5, £6, £7}. The dictator transfers an amount t ∈
{−£3, −£2, −£1, £0, £1} to the recipient, and payoffs are computed as πD = £9 – t for the
dictator, and πR = E + t for the recipient. Thus, in both the Give and Take version of the
games, dictators can implement exactly the same final payoff allocations between
themselves and recipients. However, the Give and Take games differ in whether these
allocations can be obtained through “giving to” or “taking from” the recipient. For each
treatment and each version of the game, we conducted two types of experiments: a norm-
elicitation experiment and a behavioral experiment. The norm-elicitation experiment is
based on the task introduced by KW. Subjects were given a description of the five possible
situations faced by either D2 in the Peer treatment or the dictator in the NoPeer
treatment. We conducted separate sessions for the Give and Take versions of the games. In
each case, subjects had to evaluate, for each of the five situations, the appropriateness
of each of the five actions that were available to the dictator. For example, subjects in
the Peer/Give condition read a description of a situation where D2 observes that D1 has
given £0 to the recipient and must decide whether to give £0, £1, £2, £,3 or £4. For each
of the possible five actions available to D2, subjects were asked to rate, on a six-point
scale, whether that action was “socially appropriate” and “consistent with what most
people expect [a dictator] ought to do”, or “socially inappropriate” and “inconsistent
with what most people expect [a dictator] ought to do”.9 Similarly, subjects rated the
appropriateness of each of the five dictator actions in the other four situations where D1
had given £1, £2, £3 and £4 to the recipient.10 Similar to KW, subjects received a
monetary reward if their appropriateness judgments matched the judgments provided by other
subjects in their session. In particular, they were told that one of five possible
situations, and one of the five actions available to the dictator in that situation, would
be selected at random at the end of the session. Subjects were paid £7 (in addition to a
£5 show-up fee) if their appropriateness rating for the selected action matched the rating
of one other randomly selected subject in the session.11 Thus, as in KW, subjects were
given incentives to reveal what they perceived to be the collectively-shared judgment of
appropriateness of the actions they evaluated, and not their own personal judgment. Hence,
a subject in the norm-elicitation experiment plays 25 coordination games over
appropriateness ratings (with no feedback between games) with another randomly selected
participant.12 We conducted the behavioral experiments with subjects who had not
participated in the norm-elicitation task. Subjects were randomly assigned to either the
Peer or NoPeer treatment. In each treatment, half of the subjects participated in the Give
game, and the other half in the Take game. In all cases, we paid subjects a £2 show-up fee
in addition to any earnings made in the experiment.13 At the beginning of the experiment
we matched subjects randomly into groups and assigned a role. In the Peer treatment
subjects were matched in three-person groups and assigned the role of D1, D2, or
Recipient. In the NoPeer treatment, subjects were matched in two-person groups and
assigned either the role of dictator or recipient. Subjects then played a one-shot version
of the dictator game, either in the Give or Take frame. We elicited subjects’ choices
using the strategy method (Selten, 1967). That is, dictators in the role of D2 in the Peer
treatment and dictators in the NoPeer treatment were asked to make one decision for each
of the five possible sub-games of the game, corresponding to situations where D1 or Nature
had endowed the recipient with £0, £1, £2, £3, or £4 (£3, £4, £5, £6, or £7 in the Take
game).14 In total, we conducted 44 sessions with 850 subjects, recruited using ORSEE
(Greiner, 2015). All sessions were conducted at the University of Nottingham using z-Tree
(Fischbacher, 2007). Sessions lasted between 40 and 60 min. Table 1 summarizes the
experiment design and reports the number of subjects who participated in each treatment
and version of the game.

<h>RESULTS</h>
-------

We start by presenting the data from the norm-elicitation experiments, to examine whether
the behavior of peers influences the norms of fair sharing in our setting. We then turn to
the behavioral data, and examine whether any differences in norms across conditions
translates into differences in sharing behavior.

<hs>  Norm-elicitation experiments: the influence of peers on norms of fair sharing</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Fig. 1 reports the average ratings of appropriateness collected in the norm-elicitation
experiments. We report the full distributions of appropriateness ratings in Online
Appendix B and an analysis of the variation of ratings in Section 5.1 (Fig. 3 in
particular). The average social appropriateness ratings of dictator transfers in the Peer
treatment are shown in the top-left (Give game) and bottom-left (Take game) panels of the
figure. The ratings of the NoPeer treatment are shown in the right panels of the figure.
In each panel, we show ratings for each of the five possible situations faced by a
dictator, corresponding to the five possible levels of wealth of the recipient determined
either by D1’s transfers (Peer) or by chance (NoPeer).15 Several interesting patterns can
be observed. First, in all five situations and in all treatments and versions of the game,
the appropriateness of transfers increases in their generosity: sharing the highest amount
available (“give £4″ in Give; “give £1″ in Take) is always considered the most appropriate
option. Similarly, in all cases, the least appropriate choice is the level of sharing that
maximizes the dictator's payoff (“give £0″ in Give; “take £3″ in Take).16 Second, the
level of the recipient's wealth generally influences the perception of what constitutes an
appropriate level of sharing. These differences are, however, much more marked in the Give
than in the Take game. Thus, the norms of fair sharing in the Give game seem much more
malleable than the corresponding norms in the Take game. Third, and most importantly, the
levels of the recipient's wealth influence ratings of appropriateness differently
depending on whether these levels have been determined by the transfers of another
dictator (Peer treatment) or by chance (NoPeer treatment). In the Peer treatment giving
little to the recipient is generally viewed as less appropriate when the recipient's
wealth is large (i.e., when the peer has been generous) than when a recipient's wealth is
small (i.e., when the peer has also given little).17 However, in the NoPeer treatment the
relation between appropriateness and recipient's wealth is reversed: giving little to the
recipient is viewed as more appropriate when the recipient's wealth is large (i.e. when
Nature selects a large endowment) than when it is small.18 We examine these patterns more
formally using OLS regressions, reported in Table 2. In Model I we use data from the Peer
treatment only, whereas in Model II we use data from the NoPeer treatment only. In both
regressions, the dependent variable measures the appropriateness of the dictator's
transfers in the five different situations. We regress this on the amount that the
dictator transfers to the recipient (“Amount transferred by Dictator”), the amount that
the peer (Peer treatment) or Nature (NoPeer treatment) transfers to the recipient (“Amount
transferred by Peer/Nature”), and an interaction between these two variables. Moreover, to
gauge the extent to which the influence of peers varies across the Give and Take games, we
also include a dummy variable taking value 1 for observations in the Take game, and an
interaction between the Take dummy and the “Amount transferred by Peer/Nature” variable.
The regressions reveal that in both the Peer and the NoPeer treatments more generous
transfers by the dictator are viewed as more appropriate than ungenerous transfers. The
effect of increasing the dictator's transfer on its evaluation of appropriateness is 0.359
+ 0.019 * “Amount transferred by Peer” in the Peer treatment and 0.411 − 0.009 * “Amount
transferred by Nature” in the NoPeer treatment. In both cases, the effect is positive for
any possible amount transferred by the peer or Nature. To gauge how changes in the
recipient's wealth affect the judgments of appropriateness of the dictator's transfers, we
need to inspect the coefficients of the variable “Amount transferred by Peer/Nature” and
the interaction term “Amount transferred by Dictator * Amount transferred by Peer/Nature”
(as well as the interaction with the Take dummy, for the Take game). In the Peer
treatment, the peer's generosity negatively influences the judgments of appropriateness of
the dictator's transfers. This effect is particularly marked for ungenerous dictator's
transfers, while the influence of peers wanes for more generous dictator transfers, as
indicated by the positive and significant coefficient of the interaction term between the
“Amount transferred by Dictator” and “Amount transferred by Peer/Nature” variables. In
contrast, in the NoPeer treatment the judgments of appropriateness of the dictator's
transfers become more lenient the higher is the endowment that Nature transfers to the
recipient. Again, this effect is particularly marked for ungenerous dictator transfers and
it diminishes as dictators transfer more money to the recipient, as indicated by the
negative and significant coefficient of the interaction term. Finally, in both treatments,
the impact of the recipient's wealth on norms is significantly weaker in the Take than in
the Give game. This can be seen by noticing that, in both the Peer and the NoPeer
treatments, the coefficient of the interaction term “Amount transferred by Peer/Nature *
Take” takes an opposite sign relative to the “Amount transferred by Peer/Nature” variable.
In both cases the effect is significant at least at the 5% level. To account for the
ordinal nature of the norms data, we ran additional ordinal probit regressions. The
results are similar to those reported in Table 2. Moreover, we complement the regression
analysis from Table 2 by a further specification in which we pool the data from the Peer
and NoPeer treatment and include a Peer treatment dummy as well as all relevant
interactions. The results show that the differences between the Peer and NoPeer treatment
discussed above are highly significant. Both supplementary regression tables are presented
in Online Appendix D. Taken together, these results show that the behavior of peers can
have a strong, systematic influence on the perception of what constitutes a norm of fair
sharing in our setting. What are the behavioral implications of these results? Assume
that, as in the model sketched in Section 2, individuals trade off monetary payoff and
norm-compliance utility, whereby individuals gain utility from choosing actions that are
viewed as socially appropriate and suffer a disutility from choosing socially
inappropriate actions. Within this framework, one would expect a negative effect of the
recipient's endowment on giving in the NoPeer treatment: norm-compliant dictators should
be more generous when the recipient possesses a small endowment because then ungenerous
transfers are more inappropriate (and hence result in stronger disutility) than when the
recipient has a large endowment. In contrast, one would expect a positive relation between
the peer's and the dictator's transfers in the Peer treatment. In this case, ungenerous
transfers are more appropriate when the recipient is poorer than when the recipient
receives a larger transfer from the peer. Moreover, we would expect these effects to be
stronger in the Give than in the Take version of the game. We summarize these behavioral
predictions as follows: Hypothesis 1: In the NoPeer treatment, dictator's transfers
correlate negatively with the recipient's initial wealth. Hypothesis 2: In the Peer
treatment, dictator's transfers correlate positively with the amount that the recipient
received from the peer. Hypothesis 3: These effects are stronger in Give than in Take
games. In the next sub-section we present the data from our behavioral experiments to
examine the extent to which the observed variations in social appropriateness of transfers
translate in differences in behavior.

<hs>  Behavioral experiments: the influence of peers on sharing behavior</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Fig. 2 shows the average monetary transfers made by dictators in the Peer (left panel) and
NoPeer (right panel) treatments across the five possible sub-games of the game. In each
panel the figure reports the average transfers made in the Give (dark bars) and Take
(light bars) versions of the games. In the Take game, transfers have been rescaled to give
a score between £0 and £4, to ease comparability with the Give game.19 The figure shows
that there is on average no clear relation between the dictator's transfers and the
recipient's wealth in the Peer treatment, both in the Give and Take versions of the games.
Thus, whether or not the peer is generous with the recipient does not seem to affect the
dictator's sharing decisions. In contrast, a negative relation between dictator's sharing
and recipient's wealth seems to emerge in the NoPeer treatment, in both versions of the
game. Thus, dictators seem to behave less generously towards recipients that have randomly
received larger endowments. Table 3 reports OLS regressions of dictator's transfers on a
variable measuring the amount that the peer (Peer treatment) or Nature (NoPeer treatment)
transfers to the recipient, a dummy variable taking value 1 for observations in the Take
game, and an interaction between the two variables. Similar to Table 2, we run separate
regressions for the Peer treatment (Model I) and the NoPeer treatment (Model II). Model I
confirms that there is on average no evidence of peer effects in the Give version of the
Peer treatment: the amount transferred by the peer has no significant influence on the
amount transferred by the dictator (p = 0.914). This similarly holds in the Take version,
as indicated by the insignificant coefficient of the interaction term “Amount transferred
by Peer/Nature * Take” (p = 0.727). In contrast, the recipient's wealth is negatively
related to the dictator's transfers in the Give version of the NoPeer treatment. Model II
shows that increasing the recipient's wealth by £1 reduces the dictator's giving by about
£0.30, and the effect is significant at the 1% level. This negative relation between
recipient's wealth and giving is not different across the Give and Take versions of the
game, as indicated by the insignificant coefficient of the interaction term (p = 0.858).
These results are only partially in line with the results of the norm-elicitation
experiment. The negative relation between recipient's wealth and dictator's transfers in
the NoPeer treatment is consistent with Hypothesis 1. However, the results of the norm-
elicitation experiment also suggest that we should observe a positive relation between
recipient's wealth and dictator's transfers in the Peer treatment (Hypothesis 2). Our data
do not support this conjecture. Moreover, the norm-elicitation experiment suggests that
the norm of fair sharing may be more malleable in the giving than taking setting
(Hypothesis 3). However, we do not observe any difference between Give and Take games in
the extent to which the recipient's wealth affects dictator's sharing. More generally, we
see only small differences in dictator's behavior between the Give and Take games, and
only in some subgames of the Peer treatment. This is interesting because KW have shown
that using give/take frames in dictator games can produce strong differences in behavior.
However, we cannot replicate this result: in our NoPeer treatment, which is most similar
to the games used by KW, we do not observe any difference in dictator sharing between Give
and Take games, despite the existence of differences in the norms that apply to these
games (see Online Appendix C for further detail).

<h>EXPLAINING THE EXPERIMENTAL DATA</h>
--------------------------------

What can explain the observed discrepancies between the norm-elicitation and behavioral
experiments? One striking aspect of the behavioral data is that we observe substantial
heterogeneity at the individual level in the extent to which dictators are influenced by
the level of wealth of recipients (see Online Appendix D for more details). About half of
the dictators are not affected by the recipient's wealth and opt for the same monetary
transfer across all five sub-games. A third of dictators reduce their transfer as the
recipient's wealth increases, whereas about a tenth of dictators respond positively to
increases in the recipient's wealth. Our findings are similar to those reported by
Panchanathan et al. (2013) in a three-person dictator game that is closely related to our
Peer/Give treatment. They find that about half of dictators do not respond to variations
in the peer's behavior, a third give more when the peer gives less, and thirteen-percent
give more when the peer gives more. This suggests that there may be substantial
heterogeneity in the extent to which dictators are willing to comply with norms of fair
sharing, or in the extent to which they recognize these norms as applicable.
Alternatively, (at least some) dictators may be driven by other types of considerations
(e.g. inequity aversion; guilt aversion), that may conflict with normative considerations
and pull behavior away from compliance with norms of fair sharing. The next sub-sections
investigate these potential explanations.

<hs>  Norm ambiguity</hs>
  ~~~~~~~~~~~~~~

A first possible explanation for our experimental results is that there may be substantial
disagreement among subjects about what constitutes a norm of appropriate behavior in our
experiments. As we discussed earlier (Section 4.1), in the absence of peers, individuals
seem to apply a Rawlsian norm of fair sharing in our experiments, whereby the
appropriateness of giving depends in part on the level of need of the recipient. When the
peer is present, a different normative consideration is introduced as individuals
recognize that the appropriateness of giving also depends on the peer's behavior (what
Cialdini, 2001 refers to as the "principle of social proof"). Our norm experiments show
that on average the principle of social proof overrides the Rawlsian norm of sharing in
the Peer treatments (see Fig. 1). Nevertheless, it is conceivable that both norms remain
active in our experiments, exerting divergent influences on behavior and potentially
explaining the weak support for the norms model in the Peer treatments. To examine this,
we take a closer look at the norms data. Recall that in the norm-elicitation experiment
subjects could rate the appropriateness of actions on a scale with three levels of
“inappropriateness” (very inappropriate, somewhat inappropriate, inappropriate) and three
levels of “appropriateness” (very appropriate, somewhat appropriate, appropriate). Fig. 3
shows the percentage of subjects disagreeing with the majority view about the
appropriateness of each action across the various situations that they rated.20 We say
that a majority of subjects rate an action as appropriate (inappropriate) if the sum of
the relative frequencies of the ratings “very appropriate”, “somewhat appropriate” and
“appropriate” is greater (lower) than 50%. The light (red) bars indicate that there is a
minority of subjects assigning one of the three levels of “inappropriateness” to an
action, while the majority rated the action as appropriate. The dark (blue) bars show
disagreement in the opposite direction (the majority view the action as inappropriate and
a minority rates it as appropriate). For instance, the first dark bar in the top left
panel of the figure shows that in the Peer/Give treatment 12% of subjects rated the action
“give £0″ as appropriate in the scenario where the peer also gives £0, indicating that the
remaining 88% of subjects rated it as inappropriate.21 To assess the presence of norm
ambiguity, consider first the NoPeer/Give treatment (top right panel). In most cases,
relatively few subjects (less than 20%) disagree on the social appropriateness of actions.
The main source of disagreement among subjects is the action “give £2″, which between one-
fifth and one-half of subjects view as inappropriate in contrast with the majoritarian
view that the action is appropriate. Nevertheless, apart from this action, the general
picture emerging from the NoPeer/Give treatment is that there is a reasonably low degree
of ambiguity about the social norm in this setting. Consider now the Peer/Give treatment
(top left panel). As in the NoPeer/Give treatment, there is little disagreement about the
actions “give £0″ and “give £4″. Also as in NoPeer/Give, subjects tend to disagree on how
to rate the action “give £2″. However, relative to the NoPeer/Give treatment, subjects
also disagree more on how to rate the actions “give £1″ and “give £3″. For both actions
there are at least some scenarios where about 40% of subjects disagree with the majority
view. Moreover, the source of disagreement seems to be related to the behavior of the
peer. For example, when the peer gives £1 most subjects view the dictator action “give £1″
as appropriate, presumably following the principle of social proof. However, 41% of
subjects disagree and rate it as inappropriate, presumably following a Rawlsian norm
similar to the one that subjects recognize in the NoPeer treatment. As another example,
the dictator action “give £3″ is generally viewed as appropriate by a majority of
subjects. However, when the peer gives £4, 42% of subjects rate this action as
inappropriate, again presumably because this action compares unfavorably with the peer's
action. Overall, the observed patterns of disagreement suggest that observing what a peer
has decided to do may introduce some ambiguity about the social norm. Finally, Fig. 3
corroborates our previous observation that the norm in the Take treatment (bottom panels)
is substantially less malleable than the norm in Give. For all actions and in both the
Peer and NoPeer condition, very few subjects disagree with the majoritarian view about the
appropriateness or inappropriateness of actions. The degree of agreement seems somewhat
stronger in the NoPeer condition, but again the differences are small. To summarize, this
qualitative analysis suggests that disagreement among subjects about what constitutes a
norm of appropriate behavior can go some way in explaining the lack of support for the
norm model in our experiments.

<hs>  Heterogeneity in norm compliance</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Another explanation for our experimental results is that there may be heterogeneity in
preferences for norm compliance in the population of dictators we sampled for our
experiment. Thus, even if norms of fair sharing were prominent and clear in the
population, not all dictators would be willing to follow these norms. Moreover, the
dictators’ willingness to follow norms may itself vary across treatment conditions. To
explore these possibilities, we follow the econometric methodology used by KW and related
papers and investigate the extent to which elicited norms can predict actual behavior in
our experiments. Differently from previous papers, we use a mixed logit model (see, e.g.,
Train, 2003) that allows for heterogeneity in the concerns for norm compliance and allows
us to estimate, for each treatment, the share of dictators that are in fact guided by a
desire to follow social norms. Table 4 presents the results of the estimation. We estimate
four different models, one for each treatment/game combination.22 In all models, the
coefficient on own payoff is positive and highly significant, indicating that dictators
are more likely to choose transfers that yield higher own payoffs. Turning to norm
compliance, Table 4 reports the mean and standard deviation of the norm rating
coefficients. Looking first at the estimates of the mean, the regressions confirm the
limited success of the norms compliance model in explaining the behavioral data. In the
Peer treatment (Models I and II) the average effect of norm ratings on the choice of
monetary transfers is not significantly different from zero: on average, dictators do not
choose transfers that are deemed more socially appropriate more often. In the NoPeer
treatment (Models III and IV) the effect is positive and significant in the Give game,
indicating that the average dictator is more likely to choose transfers that are more
socially appropriate. The effect is, however, not significantly different from zero in the
Take game.

<hs>  Other behavioral explanations: inequity aversion and guilt aversion</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

So far we have considered explanations related to the existence of heterogeneity in norm
compliance or in the understanding of what constitutes a norm. However, it is also
possible that participants are motivated by other types of behavioral considerations
instead of (or in addition to) normative concerns. Here we consider two popular behavioral
motives that may have particular bite in the context of our dictator games. First,
distributional preferences may play a role, especially because our Peer and NoPeer
treatments are based on three-person and two-person games respectively, and this affects
the implications that choices have for the redistribution of payoffs across players. For
example, when the recipient's wealth is £3 in the NoPeer/Give treatment, there is no
action by the dictator that can equalize payoffs between the two players (dictator and
recipient). However, when the recipient's wealth is £3 in the Peer/Give treatment, giving
£3 to the recipient equalizes earnings between the dictator and the peer. Previous studies
have found that payoffs of third parties have strong influences on sharing behavior, even
in settings where the payoff of the third party is completely exogenous and cannot be
affected by players’ decisions (e.g., McDonald et al., 2013). Thus, payoff comparison
considerations may explain some of the differences between the Peer and NoPeer treatments.
Can the Fehr and Schmidt model explain the patterns of choices in the behavioral
experiments? It turns out that the model does not predict behavior in either of the
treatments. In the NoPeer treatment, the model predicts no relation between the
recipient's wealth and dictator's giving. This is because in our games the dictator is
always at least as well off as the recipient, at all levels of the recipient's wealth and
for all the actions available to the dictator. This implies that the model predicts that
the dictator either gives nothing (if βi < 1/2) or gives £4 (if βi ≥ 1/2), regardless of
the wealth of the recipient. In contrast with this prediction, our data from the NoPeer
treatments show that dictators reduce their giving as the recipient's wealth increases. As
for the Peer treatment, the Fehr and Schmidt model predicts that, if D2 gives any money to
the recipient (which occurs when βi ≥ 2/3), the amount given is positively correlated with
the peer's giving. This is because, in the three-person Peer games, D2 compares her payoff
not only with the recipient but also with the peer. Thus, because of disadvantageous
inequality aversion, D2 is willing to give money to the recipient only to the extent that
the peer also gives money, so that her payoff does not fall behind the peer's payoff. Our
data do not support this prediction and show no relation between the two dictators’
actions in the Peer treatment.23 A second potential motive that may play a role in our
setting is guilt aversion (e.g., Charness and Dufwenberg, 2006). Guilt averse dictators
suffer a disutility if they leave the recipient with less money than what the recipient
expects to receive. Guilt aversion may predict differences in behavior between our
treatments because in the Peer treatments dictators may adjust their beliefs about what
the recipient expects to receive based on the giving of their peer. For instance,
observing that the peer gives £4 to the recipient may induce dictators to adjust their
beliefs upwards as they may interpret the peer's actions as a signal that the peer thinks
that the recipient expects £4 from a dictator. This signal is instead unavailable to
dictators in the NoPeer treatment. In order to test models of guilt aversion, one needs
second-order beliefs of dictators about what recipients expect to receive. This is
particularly important if one wishes to test whether these models are observationally
different from models of norm compliance (see, for example, Krupka et al., 2017). Because
our design is already quite complex, we have not elicited beliefs and so we cannot perform
a formal test of guilt aversion as a potentially distinct explanation of our data.
Nevertheless, if one plausibly assumes a positive correlation between dictators’ second-
order beliefs and peer's giving (along the lines discussed above), then a positive
relation between peer's and dictator's giving should emerge in the Peer treatments. At the
aggregate level our data do not support this prediction. In this sense, we think that
guilt aversion is an unlikely explanation of our behavioral results.

<h>CONCLUSION</h>
----------

Our study shows that the behavior of others can have important effects on the way
individuals perceive what constitutes socially appropriate behavior in a given situation.
In our dictator game experiments, whether or not an action is viewed as socially
appropriate partly depends on the extent to which another dictator (the “peer”) is willing
to take it. These strong effects of peer behavior on norms do not translate, however, into
corresponding effects in actual behavior in the aggregate. In particular, we do not
observe a positive correlation between the dictator's and peer's generosity in the
treatment where dictators receive information about peer behavior. Thus, generous peers do
not breed more generosity, despite the strong impact of peer behavior on the average
social acceptability of generous and ungenerous behavior.24 We discuss a number of
possible explanations for the discrepancies between normative considerations and actual
behavior observed in our experiments. We find evidence of heterogeneity in normative views
that is related to the presence of peers: the peer's behavior introduces normative cues
that are in contrast with the notion of fair sharing that subjects seem to hold when peers
are absent (see McDonald et al., 2013 for related evidence). This conflict in normative
views can explain why we find a large fraction of subjects unwilling to comply with the
average view of appropriateness and why dictators fail to follow the example of peers.
Thus, our results suggest that the extent to which peers reinforce or counteract pre-
existing notions of appropriateness may be an important determinant of the strength of
peer effects. Our results raise a number of interesting questions regarding the existing
approaches to norm compliance (e.g., Krupka and Weber, 2013). The current focus on
normative consensus (the average or most frequent notion of what is appropriate) may be
limiting in contexts where there are conflicting normative views: understanding the
interplay between heterogeneous norms and norm compliance seems crucial in order to
explain behavior in such situations.25 In this sense, the use of within-subject
experimental designs, where normative views and behavior are collected from the same
subjects, may prove a useful research tool for further research in this area, since they
would allow to correlate at the individual level behavior and beliefs about what
constitutes a norm in a given situation.26 Another interesting question relates to the
role of sanctions for norm compliance. Recent research has shown that individuals are
willing to use direct and indirect punishment to enforce social norms at a cost to
themselves even in one-shot interaction with strangers, and this can help explain why
norms are adhered to (Balafoutas and Nikiforakis, 2012; Balafoutas et al., 2014).
Punishment opportunities may also play a role in resolving norm heterogeneity, for
instance if subjects are willing to enforce only some of the conflicting normative views
that are present in the population, but not others. In our setting there was no
possibility of norm enforcement and so we cannot test this hypothesis in our data, but
this could be an interesting avenue for further research.


<h>REFERENCES</h>
----------

  [1] Loukas Balafoutas, Nikos Nikiforakis. Norm enforcement in the city: A natural field experiment. doi:10.1016/j.euroecorev.2012.09.008
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  [4] Cristina Bicchieri. The grammar of society: The nature and dynamics of social norms. doi:10.1017/CBO9780511616037
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  [6] Colin F. Camerer. Behavioral game theory: Experiments in strategic interaction
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  [9] Robert B. Cialdini, Raymond R. Reno, Carl A. Kallgren. A Focus Theory of Normative Conduct: Recycling the Concept of Norms to Reduce Littering in Public Places. doi:10.1037/0022-3514.58.6.1015
  [11] Armin Falk, Urs Fischbacher, Simon Gächter. Living in two neighborhoods-social interaction effects in the laboratory. doi:10.1111/j.1465-7295.2010.00332.x
  [12] Ernst Fehr, Klaus M. Schmidt. A theory of fairness, competition, and cooperation. doi:10.1162/003355399556151
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<ART>Truth-telling and the regulator. Experimental evidence from commercial fishermen
================================================================================

Authors: Moritz A. Drupp, Menusch Khadjavi, Martin F. Quaas
DOI: 10.1016/j.euroecorev.2019.103310
Year: 2019
ASJC codes: 2002, 2003
Keywords: Field experiment, Fishermen, Lying, Truth-telling

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Understanding what determines the truth-telling of economic agents towards their regulator is of major economic importance from banking to the management of common-pool resources such as European fisheries. By enacting a discard-ban on unwanted fish-catches without increasing monitoring activities, the European Union (EU) depends on fishermen's truth-telling. Using a coin-tossing task in an artefactual mail field experiment with 120 German commercial fishermen, we test whether truth-telling in a baseline setting differs from behavior in two treatments that exploit fishermen's widespread ill-regard of their regulator, the EU. We find, first, that fishermen misreport coin tosses more strongly to their advantage in a treatment where they are faced with the EU flag, and, second, that misreporting is consistent with behavior in other hidden tasks. We also find some supportive evidence for our first result in a conceptual replication with 1200 UK citizens who voted ‘leave’ in the Brexit referendum. Our findings imply that lying is more extensive towards an ill-regarded regulator and that policy needs to account for this endogenously eroding honesty base.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Although honesty is regarded as a virtue or even a moral duty (Kant, 1785), lying and
deception permeate economic life (Gneezy, 2005). Studying truth-telling has accordingly
become a focus of inquiry for economics.1 An area of particular public economic importance
is the truth-telling of economic agents towards their regulating authorities—from the
banking industry (Cohn et al., 2014), and tax reporting (Jacobsen and Piovesan, 2016;
Kleven et al., 2011) to environmental regulation (Duflo et al., 2013). The case where the
German car manufacturer Volkswagen systematically lied about cars’ emissions is but one
prominent example. Faced with uncertainty about how honest economic agents are, regulators
need to decide how much to invest in monitoring and how to devise appropriate sanctioning
schemes for misbehavior. Appropriate monitoring and sanctioning mechanisms are especially
crucial for the management of common pool resources (Ostrom et al., 1992; Rustagi et al.,
2010), with the fishery as a prime example (Wilen, 2000; Stavins, 2011). Fishery
management comes in many different forms around the globe. It ranges from stringent
restrictions on fish catches using individual transferable quotas—as in New Zealand
(Newell et al., 2005) or Iceland (Arnason, 2005)—to largely unregulated open-access
fishing, as it is still the case for most high-seas fisheries. The costs of illegal,
unreported and unregulated fishing are substantial and amount to US$ 10 to 23 billion per
year (Global Ocean Commission, 2013). Due to its economic importance and the heterogeneity
of its regulatory structures, the fishery has gained substantial interest in experimental
economic work.2 This paper extends the scope of previous studies and investigates to what
extent regulator framing affects truth-telling. Our study therefore adds a new dimension
to effective regulatory policy. We present evidence from an artefactual mail field
experiment that examines truth-telling of German commercial fishermen. German commercial
fishing is regulated by the European Union (EU), which is the world's fourth largest
producer of fish, under the European Common Fisheries Policy. The EU has recently enacted
a ban on returning unwanted fish catches to the sea (also called “discard ban” or “landing
obligation”), as the practice of discarding ensues substantial costs to the public.3 The
change in legislation has, as of yet, not been combined with more stringent monitoring.
The regulator, and scientists assessing the status of fish stocks upon which
recommendations for fishery management are based, thus depend on fishermen's truth-
telling. Continuing to discard unwanted fish catches remains the individually optimal
choice for fishermen in the present regulatory regime unless the regulator enforces the
new policy. This, however, would require costly monitoring and sanctioning mechanisms.4
This trade-off for the regulator between more costly monitoring and reliance on
regulatee's honesty is not only relevant in the fishery for the newly enacted European
“discard ban” or compliance with fishing quotas, but is present more generally, including
the previously discussed cases of banking, tax reporting and environmental regulation. For
studying to what extent fishermen might tell the truth towards their regulator, we conduct
a coin-tossing game in a mail field experiment targeting all commercial fishermen in
Germany. Adapting the 4-coin toss game of Abeler et al. (2014), we ask fishermen to toss a
coin 4 times and report back their number of tail tosses. For each reported tail toss,
they receive five Euros. In a between-subjects design, we test whether truth-telling in a
baseline setting differs from truth-telling in two further treatments with different EU
framings, where, first, the EU flag is made salient on the instruction sheet, and, second,
a framing that states additionally that the European Commission has funded the research.
Based on a simple model of reporting behavior of fishermen that considers internal Nash
bargaining among a pay-off maximizing ‘selfish self’ and a ‘moral self’, we hypothesize
that the salience of the EU regulator may increase the bargaining power of the ‘selfish
self’ vis-à-vis the ‘moral self’ and thus decrease overall lying costs if the EU is ill-
regarded. The fishery is an ideal test case for studying how truth-telling behavior may be
affected by regulatory framing, as there is well-documented and wide-spread contempt among
fishermen concerning stricter EU fishing regulation. We confirm the almost entirely
negative view of the EU prevalent among European fishermen (documented for UK fishers by
McAngus, 2016) for our field experimental setting in Germany: Besides ample anecdotal
evidence, our survey results indicate that the vast majority of participating fishermen
have a low trust in the EU, while this is only the case for about a third of a student
control group. If regulator framing impacts truth-telling, we will therefore expect an
almost uniform direction of the effect. To study the robustness of our findings, we
conduct a similar experiment with a population that is similar to the fishermen with
respect to the (negative) stance towards the EU: Brexiteers. Using a large sample of UK
citizens we conduct the experiment with 1200 individuals who reported to have voted
‘leave’ in the Brexit referendum in previous questionnaires. We find that fishermen
misreport coin tosses to their advantage, albeit to a lesser extent than standard theory
predicts. As hypothesized, misreporting is larger among fishermen who are faced with the
EU flag. Our main effect is supported by further regression analyses. We also find some
support for our main result in the conceptual replication with Brexiteers. Furthermore, we
find that misreporting by fishermen is consistent with behavior in other hidden tasks
involving a sent-along coin and the possibility to cheat in a competition task, suggesting
some more general validity of the coin toss findings. Overall, our results imply that
lying is more extensive towards an ill-regarded regulator. We close by discussing further
policy relevance of our results.

<h>FIELD SETTING, EXPERIMENTAL DESIGN AND HYPOTHESES</h>
-------------------------------------------------

The fishery has economic relevance in the German coastal regions at both the North Sea and
Baltic Sea. According to the European Union's Common Fisheries Policy (CFP), the Council
of Ministers of the European Union and the European Parliament set fishing quotas for the
German fisheries. The German Federal Office for Agriculture and Food distributes the
national catch quotas to fishing organizations or individual fishermen. Monitoring and
enforcement of compliance are the duty of EU member states, and ultimately of the federal
states in the case of Germany. A total of 896 commercial fishermen, owning 1465 fishing
vessels (German Fishery Association, 2015), are registered at the German Federal Office
for Agriculture and Food as holders of catch permits for the North Sea or Baltic Sea.
Cutter type trawlers and coastal vessels constitute the core of the fleet with 300 boats.
Small coastal fishing with passive gear such as gill nets and fish traps on vessels of
less than 12 m length, composed of 1139 vessels, is predominantly operated at the Baltic
coast. The German fishing fleet also includes seven deep-sea trawlers and two special
vessels for pelagic fishing that operate in long distant waters, and 46 shell- and other
special boats. Fig. 1 depicts a map of Germany's coastal regions, where the red balloons
indicate the zip codes of fishermen who have participated in the experiment. The recent
economic literature on honesty and lying has substantially advanced our understanding on
what determines when and to what extent individuals lie. Abeler et al. (2019) conduct a
large-scale meta-analysis of studies using coin-tossing and die-rolling tasks. This meta-
analysis shows that, on average, individuals lie to some, but not to an exhaustive, extent
and that the extent of lying does not seem to increase with the stakes. This paper
contributes a new dimension to the analysis of truth-telling behavior: by studying how the
salience of the regulator, who depends on truth-telling behavior in the policy context,
affects the behavior of those being regulated. To this end, we adapt the 4-coin-tossing
game of Abeler et al. (2014) for our mail field experiment. The fishermens’ task was to
toss a one Euro coin exactly 4 times, and report their result in a table printed on the
instructions sheet. For each instance they reported that the winning toss “tails” (in
German “Zahl”, meaning “number”) laid on top, they received 5 €. A key feature of this
task is that lying can be detected on aggregate when examining the distribution of
decisions, but not on the individual level. Thus, depending on luck and honesty, each
fisherman received between 0 and 20 € for this task. Besides the different sample pool, a
major difference to the previous study is that Abeler et al. (2014) conducted their 4-coin
experiments via telephone or in the lab and the decision whether to report truthfully or
to cheat was immediate, while our subjects had several weeks to decide on whether to
report honestly or to lie. In addition to previously studied effects, we hypothesize that
the salience of the regulator affects individual lying costs. Salience of the regulator,
in this case the EU, may decrease (increase) the ‘selfish self's’ bargaining power αi if
the EU is well (ill) regarded. In our experiment we take advantage of the well-documented
and wide-spread contempt among fishermen concerning stricter EU fishing regulation over
the past decade.8 That is, we unambiguously predict an increase in the ‘selfish self's’
bargaining power αi if the salience of the regulator matters for truth-telling.9 In order
to test our prediction, we sent out three versions of the instructions in a between-
subjects design: (i) a baseline setting (‘Baseline’) in which only the logos of our two
institutions present on the letterhead, (ii) a version where the EU flag is made salient
in the letterhead of the instruction sheet (‘EU_Flag’), and (iii) an additional treatment
where the framing states that this research has been funded by the European Commission
(‘EU_Flag_Funding’). These framings were included on all three experimental sheets.10 Fig.
2 depicts the three letterheads and Appendix A includes the experimental instructions.
Based on the insights from previous studies on lying behavior summarized in Abeler et al.
(2019) and our treatments regarding the new regulatory dimension, we test three main
hypotheses: Fishermen report greater tail-tosses than the truthful distribution, but do
not fully misreport in the Baseline treatment. The standard economic hypothesis of pure
selfishness is that fishermen report their own payoff-maximizing option, i.e. every
fisherman would report 4 times tails. This hypothesis has been called into question by
recent empirical evidence on various lying costs (e.g. Fischbacher and Föllmi-Heusi, 2013;
Gneezy et al., 2018; Abeler et al., 2019). We therefore expect that fishermen, on average,
report coin toss results in between the expected outcome of 2 times tails if all fishermen
reported truthfully and the payoff-maximizing outcome of 4 times tails. Explanations for
not reporting four winning tail tosses may include individual lying costs and internalized
reputational costs for the profession. It may also mirror fishermen's professional
behavior of misreporting somewhat instead of lying to the full extent, for example
declaring some part but not all of their bycatch. Fishermen report less truthfully in the
EU_Flag treatment compared to the Baseline treatment. As documented above, there is
evidence for a widespread antipathy towards the EU among German fishermen, as most of new
regulations by the EU have been regarded as burdensome for the fishermen. This makes the
context of our study very useful to test Hypothesis 2, compared to cases in which the
attitude towards the regulator is ambiguous. We therefore hypothesize that the presence of
the EU flag will increase the bargaining power of the ‘selfish self’ relative to the
‘moral self’ thus decreasing lying costs and that fishermen in this treatment will thus
report less truthfully out of ill-regard towards their regulator. Fishermen may also
perceive the difference in the Baseline and the EU_Flag treatment as a difference in
wealth of the specific institutions and the research institutions being backed by the EU.
This may affect truth-telling, as previous research has shown that costs to others matter
for lying behavior (e.g. Gneezy, 2005). In an attempt to disentangle this effect from the
direct effect of a particular attitude towards their regulator, we include the third
EU_Flag_Funding treatment. Fishermen report even less truthfully in EU_Flag_Funding
compared to the EU_Flag treatment. We hypothesize that fishermen may regard the additional
informational cue as an indication that there is plenty of funding available to those
conducting the study. This may reduce the moral cost of lying, reducing the ‘misreporting
aversion’ of the ‘moral self’, and lead fishermen to report less truthfully. Fishermen may
also regard the provided information as an opportunity to acquire some of the EU's funds
to compensate for the regulatory burdens imposed on them, thus giving more bargaining
power to the ‘selfish self’, and leading fishermen to report less truthfully as well. We
show below that the experiment rejects hypothesis 3. We come back to this issue and
possible hind-sight explanations in the discussion in Section 5. To examine truth-telling
of fishermen towards their regulator, we targeted all commercial fishermen in Germany in a
mail field experiment. Due to rigorous data protection by the German Federal Office for
Agriculture and Food, the address data of fishermen were not available to us. For the
purpose of our study, the Thünen Institute of Sea Fisheries, the national fishery research
institute responsible for carrying out fishery surveys, sent out the study documents to
all 896 fishermen on our behalf. We prepared the envelopes with the survey materials,
including stamped return-envelopes, at the University of Kiel. We then delivered the
envelopes to the Thünen Institute and were present when the address data was added. The
envelopes were sent out on Friday, December 4, 2015, and the closing date for the
experiment was January 31, 2016. We assigned anonymous ID numbers to 1200 prepared
surveys, which were numbered according to their treatment cell. After having randomly
shuffled all envelopes, 896 of these envelopes were sent out to fishermen by the Thünen
Institute.11 The experiment material consisted of 7 pages, including a cover letter, three
experimental tasks with one page each, a two-page questionnaire and a sheet for payment
information. Appendix A contains an English translation of the material. Besides the coin-
tossing task, it includes an experimental task to elicit fishermen's risk preferences, and
an experimental task on competitiveness.12 Fishermen were told that the payment for
participating in the study was limited to 100 €, with an expected payoff of 50 € for
around 30 min of work. Payment was made via bank transfer or by check via regular mail. To
ensure availability of a coin to toss, we enclosed a 1 € coin that we stuck on the page of
the task (see Appendix B). We complement our main study with three additional data
collection exercises to examine its relationship to the economic literature on lying and
its robustness. First, regarding the relationship to the literature, we examine how our
subject pool of interest—professional fishermen—relate to the conventional subject pool of
university students. We therefore ran the Baseline treatment of our mail experiment also
with 50 business and economics undergraduate students at the University of Kiel at the
same time, 44 of whom participated.13 Second, to examine the robustness of our results
regarding possible attrition issues we ran an additional online experiment with 717
student subjects from the University of Kiel subsequent to the main study including two
treatments: positive and negative framing regarding the fishery policy of the European
Union and its effect on trust towards the EU. The reason is that mail field experiments
may suffer from substantial attrition and we are not able to rule out by design that
attrition in our fishermen study may depend on the treatment. The additional online
experiment allows us to investigate the potential importance of attrition for the
treatments in our main study and offers secondary causal insights into the effect of
positive and negative framing of the policy on trust in the European Union. Third, to
conceptually replicate and further investigate our main hypotheses and potential
confounds, we conducted another online experiment with 1200 Brexit voters. We describe the
details of this additional experiment in Section 4.

<h>RESULTS</h>
-------

We received 136 responses by fishermen, amounting to an overall response rate of 15%.14 Of
those, 120 responses included results for the coin-tossing task (see Table 1 for
descriptive statistics),15 which were provided by fishermen located in 58 different
ports.16 Aggregating all of our three treatments, we find that overall reporting by
fishermen differs significantly from the truthful distribution as well as from payoff-
maximization: fishermen report to have tossed 2.46 winning tails on average. This
indicates substantial lying costs in line with the previous literature. A fraction of
10.83% of fishermen report that they have obtained four times tails, and 42.50% report
three times tails. The distribution of reported outcomes is statistically highly
distinguishable from both the payoff-maximizing outcome as well as from the truthful
distribution. Two-sided binomial tests of the expected truthful against the observed
frequency for 3 tails and for the payoff maximizing decision of 4 reported tails yield p =
0.000 and p = 0.055, respectively. In particular, we find reporting of 3 tail tosses at
the expense of reporting 0 or 1 coin toss. The latter differs from the truthful
distribution significantly (two-sided chi-squared test on combined 0 and 1 reports: p =
0.000). We therefore confirm Hypothesis 1 and previous findings in the literature. Next,
we analyze the effects of our treatments on truth-telling.17 Fig. 3 shows the mean
reported tail tosses across the three treatments. In the Baseline treatment, as well as in
the EU_Flag_Funding, fishermen report an average coin toss result of 2.38 winning tails.
In the EU_Flag treatment the average coin toss result was 2.64 tails. While this
qualitatively suggests that fishermen over-report tail tosses in the EU_Flag treatment as
compared to the Baseline, this is not statistically significant (two-sided t-test: p =
0.191). There is virtually no difference in mean reported tail tosses between Baseline and
EU_Flag_Funding. Next, we examine tail toss response across treatments more closely. As
Fig. 4 shows, no fisherman in the EU_Flag treatment reported 0 tail tosses, fewer
fishermen reported 1 tail tosses compared to the Baseline treatment (8.33% vs. 11.90%) and
more fishermen reported 4 tail tosses (16.67% vs. 4.76%). We find that fishermen in
EU_Flag over-report tail tosses that yield the highest payoff (two-sided chi-squared test:
p = 0.084). This finding provides some confirmation for Hypothesis 2: The salience of the
regulator does seem to play a role for truth-telling and the wide-spread ill-regard for
the EU seems to translate into stronger over-reporting of tail tosses. We find no material
and significant differences between the EU_Flag and the EU_Flag_Funding treatments in
terms of 4 tails reporting (two-sided chi-squared test: p = 0.547). However, we find that
fishermen in the EU_Flag_Funding treatment report significantly more 0 and 1 tail tosses
(combined: 23.81% in the EU_Flag_Funding vs. 8.33% in the EU_Flag treatment; two-sided
chi-squared test: p = 0.067). These findings reject Hypothesis 3. Specifically, we do not
find support for the ‘wealth-of-funding-institutions’ or ‘taking-back from the EU’
hypotheses as fishermen in the EU_Flag_Funding do not report more 4 or combined 3 and 4
tail tosses. We discuss this finding in Section 5. To further scrutinize hypotheses 2 and
3, we run a regression analysis of overall tail toss reporting with the two treatments and
additional controls (see Table 2). Specification (1) includes all eight covariates that
are significantly correlated with tail toss reporting in univariate regressions.
Specification (2) also includes the standard demographic variables income and education
level as additional controls. Since many fishermen did not respond the question on the
probability of their income increasing over the next five years, which causes the low
number of observations in specifications (1) and (2), we run an additional regression
specification (3) dropping this variable. The regression analysis shows that across the
three specifications EU_Flag_Funding changes sign. Indeed, we find that it is very far
from significantly explaning different overall tail toss reporting compared to the
baseline, with p = 0.808, p = 0.543 and p = 0.784, respectively. We find that the only
consistently significant explanatory of variable of tail toss reporting is the EU_Flag,
with a p-value in specification (1) of p = 0.022, in specification (2) of p = 0.005, and
in specification (3) of p = 0.074. This provides further support for our Hypothesis 2. We
summarize Fishermen over-report more severely when facing the EU flag. Our study also
included two novel ‘hidden’ tasks that offer the possibility to underscore truth-telling
or lying behavior. First, we deliberately left the ownership about the one Euro coin that
we included on the coin tossing decision page unclear. A related aspect of fishermen's
fidelity is thus whether they sent back the coin with their decision sheets. We find that
the 22 fishermen who sent back the coin report a coin toss result of 2.23 tails on
average, compared to 2.51 tails for those who did not send back the coin (see Fig. C.1 in
Appendix C). This difference is not significant (two-sided t-test: p = 0.205), yet
tentatively suggests consistent behavior between the coin-tossing task and this hidden
measure and therefore some external validity. Second, we conducted a separate task to
measure fishermen's competitiveness using a real production task where fishermen have to
produce paper shreds by hand from an A7-sized (74 × 105 mm) piece of paper. Fishermen
decided on whether they want to be paid 0.05 € per piece, or whether they want to play
competitively and receive 0.15 € per piece if they perform better than a randomly drawn
other participant. As the A7-sized paper we sent the fishermen was of standard white
format, dishonest fishermen could add additional alien paper shreds to increase their
payoffs. To control for this possibility to cheat, we measured the weight of the returned
paper shreds on an analytical scale from the physical chemistry lab. We find that the 10
heaviest envelopes with paper shreds, i.e. those where paper shreds have been added most
likely to unduly increase payoff, report a mean coin toss result of 3.00 tails, compared
to 2.41 tails for the rest (t-test: p = 0.062).18 We summarize these two indicative
findings as: (Mis-)Reporting in the coin-tossing task is consistent with behavior in
hidden truth-telling tasks. These findings are in line with growing and distinct evidence
on the external validity of experimental lab measures of truth-telling in the literature
(Cohn and Maréchal, 2018; Cohn et al., 2015; Dai et al., 2018; Gächter and Schulz, 2016;
Potters and Stoop, 2016). Our indicative finding, together with the mounting evidence in
the literature, therefore suggests that the coin-toss truth-telling measure is informative
of fishermen's honesty behavior in the field. Next, we compare fishermen in the Baseline
treatment with our student sample that faced the exactly same study design as the
fishermen (see Fig. 5). As outlined in the previous section, we collected this data to see
how our fishermen subject pool relates to the conventional student subject pool. While
fishermen reported to have tossed 2.38 tails on average, students report 3.14 tails on
average, which is significantly higher (two-sided t- test: p = 0.000).19 This result
points to the importance of using our subject pool of fishermen to answer our research
questions regarding fishery policy. Inspired by the quote of McAngus (2016) at the
beginning of our paper, we were also interested to see how the reported trust in the
European Union (specifically the European Commission), measured on a Likert scale from 1
to 9, compares between our fishermen and students. Our findings reflect the spirit of
McAngus’ quote: the average trust in the Baseline treatment of the fishermen in the EU is
2.29 compared to 5.05 of the students. We find no significant differences in the reported
trust levels among fishermen across the three treatments (pairwise t-test: p > 0.60 for
all cases). Fig. 6 depicts the distribution of trust towards the EU for all fishermen
versus the students. We see that almost half of the fishermen report a trust level of ‘1’,
the lowest possible answer on the scale. The two distributions are highly different from
each other (two-sided Kolmogorov–Smirnov: p = 0.000). From the distributions in Fig. 6, it
is evident that there is heterogeneity of students’ trust in the EU (while the fishermen's
trust is skewed). We took advantage of this observation to run an additional online
experiment with students from the same university (as outlined in Section 2). This online
experiment serves the purpose to investigate the impact of trust in the EU on attrition.
As noted in the experimental design, mail field experiments may suffer from attrition. As
we cannot rule out effects of our treatments on the extensive margin by design, i.e. that
participants selected on responding not independently from the random treatment
assignment, an alternative explanation for our findings would be that there is a fixed
proportion of honest and dishonest fishermen and that the honest participants were less
likely to send in the study when being confronted with the EU flag. To study whether the
EU framing may induce attrition, we collected additional data from 717 student subjects in
the online experiment. We randomly assigned the subjects into two treatments: positive EU
framing and negative EU framing. In both treatments we provided subjects with true
information regarding the EU fishing policy. The difference was that in the positive EU
framing treatment the regulatory efforts of the EU fishery policy were framed as a success
and in the negative EU framing treatment the regulatory efforts of the EU fishery policy
were framed as a failure.20 To reinforce the strength of the framing, we subsequently
asked subjects to report positive (negative) own experiences with EU regulations.
Thereafter we asked subjects to report their trust (a) in the European Commission, (b) the
federal German government and (c) the government of their German state.21 This exercise
yields two key insights. First, we find that subjects in the positive EU framing treatment
report to trust the EU significantly more than subjects in the negative EU framing
treatment (two-sided Kolmogorov-Smirnov test: p = 0.017).22 Fig. 7 depicts these results.
Thus, the framing seems to have worked and we can examine how it may impact attrition.
Second, we found overall attrition of only 1.25% (from 717 to 708 participants).
Crucially, there is no significant difference between the attrition in the two treatments
(two-sided chi-squared test: p > 0.1). While this finding provides suggestive evidence
that attrition does not depend on the sort of framing (positive or negative) regarding the
EU, it does not preclude the possibility that attrition in our main experiment with
fishermen has been treatment-specific.

<h>CONCEPTUAL REPLICATION WITH BREXITEERS</h>
--------------------------------------

To study the robustness of our results and possible mechanisms for regulator framing, we
conducted a second online experiment. As it is difficult to get access to addresses of
fishermen for studies and as we had already contacted all commercial fishermen in Germany
for our main experiment described above, the aim was to find a group of individuals who,
like fishermen in Germany, are known for not being fond of the EU as a regulator. We
identified Brexiteers as such a candidate and accessible population, who may not have the
same close regulatory experience with the EU as fishermen but are certainly know for not
being fond of the EU. The platform Prolific (www.prolific.ac) offers the opportunity to
run online studies with a fairly large and diverse UK population (N>20,000) and the
platform pre-collected information on subjects’ self-reported Brexit votes (‘leave’,
‘remain’ or no vote). This gave us the opportunity to run a conceptual replication and
extension of our initial study with up to 4064 potential subjects who had previously
stated that they voted ‘leave’ in the Brexit referendum. The subsections below describe
the experimental design and the results of our conceptual replication.

<hs>  Design</hs>
  ~~~~~~

In our conceptual replication with Brexit voters we used the same 4-coin-tossing task of
Abeler et al. (2014) that we also used in our main experiment with fishermen. For each
instance they reported that the winning toss “tails” laid on top, they received 1 GBP.
Thus, each subject received between 0 and 4 GBP for this task, in addition to a 2 GBP
participation fee. Following a few introductory questions, we used similar headers for the
screen of the coin tossing task on the website in the new Brexiteers_Baseline and
Brexiteers_EU_Flag treatments as in the Fisher_Baseline and Fisher_EU_Flag treatments with
the fishermen, except that the headers were slightly larger in relation to increase the
visibility on the computer screen. Based on inconclusive evidence regarding the
Fisher_EU_Flag_Funding treatment in our main study, we included a third Brexiteers_Funding
treatment, in which we displayed a text informing the participants that the study is
funded by public research funds – yet the Brexiteers_Funding treatment does neither
include any mentioning of the EU nor any EU flag. The Brexiteers_Funding treatment aims at
disentangling the effects of providing information on research funding from the EU flag
effect. Figure E.1 in Appendix E displays the three screen headers of the coin tossing
task. We included further follow-up questions to investigate potential mechanisms that
might drive treatment effects. First, our replication includes three variables on negative
reciprocity adapted from Falk et al. (2018). We included these variables to reveal
possible mechanisms for why individuals who dislike or mistrust the EU are reporting
higher tail tosses in the EU_Flag treatment (and are therefore more likely to lie in this
treatment). Second, as a potential confound that might drive treatment differences we
investigate experimenter demand effects (Zizzo, 2010; De Quidt et al., 2018). To this end,
we included the following question in as a follow-up: “How strongly do you feel that the
researchers of this study wanted you to report in a particular way in the coin task?” and
elicited responses on a 9-point Likert scale from 1 (not at all) to 9 (very strongly).
Finally, even though Prolific allowed us to pre-screen for Brexit voters, we asked
participants of our replication study whether they voted ‘leave’ in the referendum and
whether they would still vote for some form of ‘leave’ (Hard Brexit or PM Theresa May's
Leave Deal). We based the number of observations (N) in this conceptual replication with
Brexit voters on a power calculation that is informed by the effect size of the EU_Flag
versus Baseline treatment on coin toss results in our main experiment with fishermen. The
power calculation informed us that it would be necessary to collect 173 observations per
treatment in order to replicate the fishermen's effect.23 With three treatments, this
would yield N = 519. Due to the differences between our fishermen experiment and this
replication, we decided to increase N by spending up to our budget constraint of 8000
Euro, and to pre-specify hypotheses and use one-sided tests for those pre-specified
hypotheses (we use two-sided test for analyses that we did not pre-specify). In
particular, we expected that participants in such an online experiment participate in
studies more often and may take our study less seriously than the commercial fishermen.
For this reason, there are likely attention differences between our print-out mail
experiment, for which fishermen had a long time to make decisions, and the online screen
experiment for which participation times are usually very short and inattention may be an
issue. Thus, in our pre-analysis plan we set the number of observations to be collected to
N = 1200 complete responses and set this total number on the Prolific platform. The data
collection started on March 6, 2019. Subjects’ average completion time was 3.7 min (222 s)
and they received an average payment of 4.32 GBP, amounting to an hourly-equivalent
payment of 70.14 GBP. For the collection of our data, we employed the platform Social
Science Survey (www.soscisurvey.de).

<hs>  Results</hs>
  ~~~~~~~

Randomization, which was computerized through the Social Science Survey platform, yielded
almost exactly 400 observations for each of our three treatments (399, 401 and 400,
respectively). Kruskal–Wallis tests and chi-squared tests over all three treatments do not
report significant differences for any of the collected variables.24 This evidence
suggests that the randomization process worked well. We do not find significant
differences between our three treatments for the reported number of tail tosses using all
data (see Fig. 8). The average reported number of tail tosses is higher in
Brexiteers_EU_Flag than in Brexiteers_Baseline, and is therefore qualitatively as expected
and formulated in our pre-analysis plan. Yet, this difference is not significant (p =
0.267, one-sided t-test, as formulated in our pre-analysis plan). As stated in our pre-
analysis plan, we anticipated that the attention and involvement of participants of our
online experiment may be heterogeneous and that completion time can be a proxy for
(in)attention or fast-clicking. As attention and involvement may be crucial for regulator
framing to work, we stated in our pre-analysis plan that we will analyze the data for a
sub-sample that suggests a relative high level of attention and involvement. We expected
that the sample of Prolific may contain participants who just fill out items and finish
studies as fast as they can. Likewise, there may be participants who leave the screen to
do other things for some time. These participants may not have paid the required attention
to the screens and added noise to our dataset. For this reason, we proceed to analyze the
treatment effects for a sample that excludes the 10% fastest and the 10% slowest
participants, which we denote as ‘inattention truncation’.25 Fig. 8 depicts the mean
reported tail tosses between treatments both for the full sample and the inattention
truncation sample. In the next step, we conduct the (one-sided) t-tests for effects across
treatments. We find marginally significant evidence for a higher mean number of reported
tail tosses in Brexiteers_EU_Flag compared to Brexiteers_Baseline (p = 0.093). We
therefore find suggestive evidence that points into the same direction and is consistent
with Result 1 in our main experiment with fishermen. Our hypothesis in the pre-analysis
plan regarding the difference in the mean number of reported tail tosses between
Brexiteers_Funding and Brexiteers_Baseline is that there is a lower mean number in
Brexiteers_Funding. The one-sided t-test clearly rejects our hypothesis (p = 0.959).
Rather, there is evidence pointing into the opposite direction (p = 0.083, for a two-sided
t-test). As such, this does not support the tentative conclusion from the main fishery
experiment that the funding information might curb over-reporting. A third hypothesis of
ours in the pre-analysis plan was that the mean number of reported tail tosses is higher
in Brexiteers_EU_Flag than in Brexiteers_Funding. A t-test rejects this hypothesis (p =
0.656). To examine the robustness of these results and to examine the potential mechanisms
discussed above (trust in the EU, experimenter demand effects and negative reciprocity),
we run a regression analysis of overall tail toss reporting including control variables.
Table 3 reports the estimation coefficients. Specification (i) includes the treatment
dummies and the three covariates (‘age’, ‘relative income’ and ‘number of moves’) that are
pairwise significantly correlated with tail toss reporting over all three treatments.
Specification (ii), the full model, also includes all other variables collected from the
participants. The estimations show that the effect size in the multivariate regressions
for the EU_Flag treatment is much smaller in the Brexiteers sample as compared to the
fishermen. For the full model – including all variables collected from participants in our
online experiment – we find additional marginally significant evidence pointing again into
the direction that the average number of reported tail tosses is higher in
Brexiteers_EU_Flag than in Brexiteers_Baseline and also higher in Brexiteers_Funding than
in Brexiteers_Baseline.26 Overall, our replication using an online experiment with
Brexiteers provides some supportive evidence for Result 1 from our mail experiment with
fishermen. Our replication study did, however, not provide the expected explanation for
the treatment effect of Brexiteers_Funding compared to Brexiteers_Baseline. We come back
to this result in Section 5. The replication with Brexiteers also allows us to include
additional questions before and after the coin tossing task and to examine possible
mechanisms explaining mean coin toss reporting in our three treatments. Before the
Brexiteers encountered the coin-tossing task, in all treatments they were asked for their
trust in the EU. After the coin tossing task, they were further asked to state to what
extent they felt they were pushed to report the coin tossing in a certain manner (to study
experimenter demand effects) and, also after the coin tossing task, the Brexiteers were
asked to answer questions on negative reciprocity (inspired by Falk et al., 2018). For the
purpose of examining possible mechanism of our treatment effects, we dissect the mean
number of tail tosses by reporting pairwise correlation matrices for the relevant five
variables by treatment (see Tables E.2a–c in Appendix E). For Brexiteers_Baseline we do
not find any significant pairwise correlations of the five variables with the reported
number of tail tosses (Table E.2a). In our Brexiteers_EU_Flag treatment we find that one
variable correlates (marginally) positively with the number of reported tail tosses: the
answer to “Willingness to punish someone who treats me unfairly”. Hence, we get a weak
hint that negative reciprocity might be a motivation for lying in Brexiteers_EU_Flag.
Finally, in Brexiteers_Funding, we observe that all three negative reciprocity answers
correlate (marginally) negatively with tail toss reporting. A preference for reciprocity
in combination with a generally careful view on public funds might curb some lying. This
exercise neither yields any correlation between the number of reported tail tosses and
trust in the EU nor between tail tosses and perceived experimenter demand. Finally, we
briefly address attrition in our online experiment with Brexiteers. Randomization took
place when entering the treatment page and prolific only counted participants that
finished the study and came back to prolific afterwards. Of the 66 incomplete responses
that are included in the dataset, 29 dropped out immediately, 31 looked at the
introduction page but did not proceed to the next page with preliminary questions, which
only six individuals entered and four of them completed. Two of the four individuals
proceeded to the treatment page. They were allocated to the EU_Flag and Funding
treatments, respectively. These two individuals did not report a coin toss result and
stopped the survey at this point. We therefore find that treatment induced attrition might
be relevant for less than 0.2 percent of the sample, and based on the small sample we find
no indication for it. This corroborates the findings from the additional student sample on
the likely absence of treatment-specific attrition in the setting of online experiments.
However, this does not imply that treatment-specific attrition is no concern in the main
fishermen mail field experiment, as both the populations and response times differ
substantially. Indeed, we cannot rule out the possibility that some treatment differences
can be driven by treatment-specific attrition. The potential magnitude of such attrition
biases would have to be tested in future mail field experiments.

<h>DISCUSSION AND CONCLUSION</h>
-------------------------

This paper presents field experimental evidence on truth-telling of German commercial
fishermen who are regulated by the European Union (EU). To our knowledge, this is the
first artefactual field experiment with professional common-pool resource users on truth-
telling.27 Examining truth-telling of German fishermen is of direct relevance, as the
member states of the European Union stand to decide on how much costs to incur to monitor
a recently enacted ban on discarding unwanted fish catches to the sea. The regulator thus
currently depends on fishermen's honesty, while standard economic theory predicts
substantial lying behavior. This paper not only studies fishermen's overall degree of
dishonesty but extends the scope of previous studies by asking how regulator framing
affects truth-telling—a dimension that is relevant for the effective and efficient design
monitoring and sanctioning mechanisms. Our results are therefore not only relevant for the
specific fishery context, but crucial for a broader understanding of truth-telling, the
management of common pool resources around the world, and for regulatory policy more
generally. To examine the more general applicability of our findings, we also conducted a
conceptual replication and extension of our initial study with 1200 UK citizens who voted
‘leave’ in the Brexit referendum. Adapting an established coin-tossing game (Abeler et
al., 2014), where subjects have to toss a coin 4 times and receive 5 € for each of the 0
to 4 reported tail tosses, we test whether truth-telling in a baseline setting differs
from behavior in two treatments with different EU framings. The fishery is an ideal test
case for studying how truth-telling behavior may be affected by regulatory framing, as
there is almost uniform contempt among fishermen concerning stricter EU fishing
regulation. We therefore hypothesized that if regulatory framing affects truth-telling, it
would lower lying costs and thus result in higher misreporting among the treated
fishermen. We find overall that fishermen misreport coin tosses to their advantage, albeit
to a significantly lesser extent than standard theory would predict. Specifically, we find
an average reported tail toss result of 2.46, while the expected truthful distribution
would result in 2 and the payoff-maximizing choice in 4 reported tail tosses. Fishermen
thus do not lie to their maximum advantage, but partial misreporting is prevalent among
fishermen, in line with recent evidence by Abeler et al. (2019) and Gneezy et al. (2018).
Qualitatively, we find the same to be true for Brexiteers. Crucially, we find that
misreporting is larger among fishermen who are faced with the EU flag compared to the
control sample without the EU flag on the instruction sheet. Furthermore, the replication
with Brexiteers provides some supporting evidence for this main finding. This result
confirms our hypothesis according to which many fishermen (and Brexiteers) have lower
moral lying costs towards the EU, which they dislike. This indicates that previously
elicited degrees of truth-telling may not be appropriate for principal-agent
relationships, where the principal or regulator is ill-regarded by the economic agents.
Although we have found consistent evidence across our main experiment and the conceptual
replication, our central result is only borderline significant. The main study with
fishermen may be underpowered, and the replication study with Brexiteers may have suffered
from lack of attention. Future research should therefore be devoted to confirm the
generalizability of this result. In particular it would be important and interesting to
test whether the results also extend to other settings. The experiment with fishermen did
not confirm our initial hypothesis 3 that fishermen report less truthfully in
EU_Flag_Funding compared to the EU_Flag treatment. Our expectation was that fishermen may
regard the additional informational cue as an indication that there is plenty of funding
available to those conducting the study, and that this may reduce the moral cost of lying,
such that fishermen would report less truthfully. This effect is not apparent in the
experiment with fishermen. In the regression analysis, the EU_Flag_Funding treatment
variable does not explain any difference in reported tail tosses compared to the baseline
treatment. The conceptual replication with Brexiteers includes a treatment where we show
the information that this study is funded by public funds, but without the EU flag, i.e.
omitting reference to the regulator. This treatment leads to increased misreporting in a
similar way as the EU_Flag treatment. Indeed, it might be that the additional information
box about funding may make the wealth of the funding institution more salient and taking
money may appear permissible to the Brexiteers. This would be in line with our initial
hypothesis 3 formulated for the experiment with fishermen. However, the conceptual
replication did not provide an explanation why fishermen were more honest in the
EU_Flag_Funding treatment than in the EU_Flag treatment. One mechanism that may seem
plausible is that fishermen may have considered the joint information on research funding
and the EU flag as information that the EU is using money to survey fishermen. As this was
a mail experiment, fishermen may even have taken the opportunity to discuss these issues
with relatives or family members, which may have reinforced such a view. This may lead to
more support for the regulator, rendering the responses statistically indistinguishable
from the baseline treatment. However, this is just one possible explanation and there may
be others. Our findings show that the ill-regard of the regulator is not the only effect
present, and that other mechanisms may offset the dislike effect. It is an interesting
question for future research if and how the regulator can approach regulated individuals
in such a different kind of way to offset the negative attitude and thus increase truth-
telling behavior. Moreover, we find evidence suggesting some consistency of behavior
between the coin-tossing task and two other measures of truth-telling or lying behavior.
This finding is based on two hidden tasks in the experiment—leaving the ownership of a
coin to flip ambiguous and using an additional task in which it was possible to provide
more material than was supplied—that may be of use for experimental methodology beyond our
specific context to investigate the external validity of standard lying tasks. Overall,
our findings imply that regulators not only have to consider some exogenous degree of
dishonesty among the regulated, but also take into account that truth-telling may erode in
reaction to the regulatory policy. Faced with a variable degree of dishonesty, the
regulator can act strategically in adopting its regulatory approach, such as shifting part
of the regulatory work to bodies that are closer to the regulated, thus considering how
the regulated will adapt their behavior. Whereas the substantial number of fishermen who
likely report honestly might suggest that softer monitoring approaches could be
sufficient, the strategic aspect of regulatory experience calls for a more deliberate
approach. One possible solution to coping with this strategic dimension of dishonesty
would be to choose the ‘corner solution’ and comprehensive control.28 In practice, this
would mean a monitoring scheme relying on-board observers or camera systems. However,
instead of directly incurring the high costs to the regulator and fishermen of
comprehensive control, our recommended approach would be to introduce monitoring of
different degrees of stringency selectively to study the effects of monitoring on honesty.
Overall, our findings imply that lying is more extensive towards an ill-regarded regulator
and that policy needs to account for this endogenously eroding honesty base. Studying this
new dimension of truth-telling in further detail is a promising avenue for future
research.


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----------

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<ART>Unexpected school reform: Academisation of primary schools in England
=====================================================================

Authors: Andrew Eyles, Stephen Machin, Sandra McNally
DOI: 10.1016/j.jpubeco.2017.09.004
Year: 2017  |  Pages: 108-121
ASJC codes: 2002, 2003

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

The UK change of government in 2010 provoked a large structural change in the English education landscape. Unexpectedly, the new government offered primary schools the chance to have ‘the freedom and the power to take control of their own destiny’ with better performing schools given a green light to fast track convert to become an academy school. In England, schools that become academies have more freedom over many ways in which they operate, including curriculum design, budgets, staffing issues and the shape of the academic year. However, the change to allow primary school academisation has been controversial. This paper reports estimates of the causal effect of academy enrolment on primary school pupils. While the international literature provides growing evidence on the effect of school autonomy in a variety of contexts, little is known about the effect of autonomy on primary schools (which are typically much smaller than secondary schools) and in contexts where the converting school is not deemed to be failing or disadvantaged. The key findings are that English primary schools did change their mode of operation after the exogenous policy change, utilising more autonomy and changing spending behaviour, but this did not lead to improved pupil performance.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Since 2010, the educational landscape in England has radically altered. By 2017, nearly
two-thirds of secondary schools and over a fifth of primary schools are academies. Academy
schools are granted considerable operational autonomy by government and have a battery of
freedoms they can use that standard state schools cannot. As Michael Gove, the Minister
then responsible for education, put it by enabling academisation these schools have been
‘given the freedom and the power to take control of their own destiny’.1 Although
academies were present before then – principally as a school improvement policy for
underperforming secondary schools since 2002 – the programme was radically altered and
significantly expanded following the election of the new UK government in May 2010. It
became a school structure to which all schools were invited to aspire as enabling
legislation – the Academies Act of 2010 – was rapidly put in place two months after the
election of the new government.2 For the first time, and through this completely
unexpected policy change,3 primary schools were invited to become academies, with better
performing schools being given priority to convert. The first batch of such schools
converted in the school year beginning in September 2010. This paper reports estimates of
the impact of primary school conversion to academy status on their operation and on the
performance of enrolled pupils. This introduction of primary academies took place in an
international context where publicly-funded autonomous schools have become a familiar form
of school improvement policy, most notably through charter schools in the US and free
schools in Sweden. Research on the former tends to find achievement gains associated with
charter status and with the ‘injection’ of charter school features to public schools,
particularly in urban settings where the schools typically enrol disadvantaged students.4
In the Swedish context, there is some evidence of positive short and long term effects of
the free school program, but these are found to work primarily through competition (see
Bolhmark and Lindahl, 2015). The policy studied here differs from most others in the
literature in three important respects. Firstly, it involves conversion of existing
schools rather than the creation of new schools.5 Secondly, it is about the voluntary
conversion of better performing schools and not the forced conversion of failing schools.
These better performing schools very clearly have a lower proportion of children from
disadvantaged backgrounds. Thirdly, the focus is on young children (aged 7–11) who attend
primary schools, which are much smaller than secondary schools.6 Although there have been
studies of elementary schools in the charter school context, these are less prevalent than
studies of middle and high schools. Similarly, studies of autonomy in the context of the
English education system have focused on particular subsets of secondary schools;
specifically, advantaged secondary schools voluntarily gaining greater autonomy (Clark,
2009), disadvantaged secondary schools (Eyles and Machin, 2015), and secondary schools in
relatively disadvantaged local authorities (e.g. Birmingham in the case of Bertoni et al.,
2017). Upon conversion, academy schools gain autonomy over many process and personnel
decisions. This greater freedom may have positive effects on student outcomes because of
superior information held by local decision makers (Hanushek and Woessmann, 2011). Indeed,
the first secondary schools in England to become academies (in the early 2000s) did seem
to deliver positive effects on student outcomes (Eyles and Machin, 2015; and Eyles et al.,
2016a, 2016b). However, the context was one in which a couple of hundred (previously
significantly underperforming) secondary schools became academies. It is not necessarily
the case that these positive effects carry through to better performing schools and/or to
(much smaller) primary schools. If the autonomy offered within the academies model was
unambiguously advantageous for schools, one would imagine that all schools would want to
become academies. However, recently the UK government has had to back out of a policy to
force all schools in England to become academies by the end of 2022 because of fierce
hostility to this by the educational establishment (although the current government vision
is still to encourage all schools to become academies). Whether such radical upheaval is
in the interests of students is an empirical question. Most schools yet to convert are
primary schools, which represent the vast majority of schools in England. One might
hypothesise that schools which volunteered to convert to academy status early-on are those
that were most amenable to academy status, anticipating positive benefits. If effects are
not found for such schools, one might question whether it is such a good idea to extend it
to schools that are less enthusiastic. An important feature of the policy being studied
here is that it was in no way anticipated by schools or parents. This gives leverage to
identify causal effects since the conversion was exogenous to pupils already enrolled in
the school. Thus, the sample studied is restricted to these “legacy enrolled” pupils who
can be observed before and after academisation takes place. The importance of estimating
effects for pupils who were already enrolled in the school prior to conversion emerges
because student mobility post-conversion is potentially endogenous to the policy itself.
For example, parents may be attracted by the idea of academy status and be more likely to
enrol their children to newly converted primary schools. Exit from the school post-
conversion might also be non-random (for example, if schools change policies in a way that
is less attractive to certain students or their parents). However, in the empirical work
discussed below, a very strong first stage estimate (of the effect of pre-conversion
enrolment on the probability of attending an academy) suggests that a causal effect of
academy attendance is identified for the majority of eligible pupils in the school. In
practical terms, the empirical strategy adopted in this paper first involves selection of
treatment and control groups of schools. The treatment group consists of primary schools
that converted to academy status between 2010/11 and 2014/15. In each case, the control
groups are those that converted in later academic years, but before 2016/17. Under certain
conditions, these treatment and control schools are shown to have similar pre-trends in
outcome variables. Further, enrolment in the primary school prior to conversion is used as
an instrument for actual attendance in the academy in grade 6 when national tests in
reading and maths take place. The legacy enrolment strategy mirrors that used in Eyles and
Machin (2015) in their study of the first underperforming English secondary schools to
become academies in the early 2000s. It also draws on Fryer (2014) who looks at the effect
of injecting charter school practices into traditional public schools and Abdulkadiroglu
et al. (2016), who study school takeovers in New Orleans, referring to pupils who stay in
converting schools as ‘grand-fathered’ pupils. The rest of the paper is structured as
follows. Section 2 describes primary education in England and offers a discussion of the
institutional features characterising the introduction of academy schools. Section 3
describes the data and research strategy. Section 4 reports results from the first part of
the empirical analysis, looking at whether primary schools that became academies did in
fact change their modes of operation upon conversion. Section 5 reports the legacy
enrolment results looking at causal effects of academy conversion on pupil performance.
Conclusions are given in Section 6.

<hs>  Primary education</hs>
  ~~~~~~~~~~~~~~~~~

In England, children start school in the September after they reach the age of 4. Most
children attend a primary school up to age 11, after which they go to secondary school.7
Schooling in England is organised into Key Stages. At the end of Key Stage 1 (age 7),
pupils are assessed by their teachers in English and maths according to national
guidelines. At the end of Key Stage 2 (age 11), they undertake national tests in English
and maths.8 These tests are used to construct Performance Tables for primary schools,
which are publicly available. There is next to no grade repetition within the system. Up
until the introduction of academies in 2010, schooling had been organised at the local
level into Local Education Authorities (LEAs). There are 152 LEAs in England and around
15,000 primary schools. The LEA's main functions in relation to primary schools are in
building and maintaining schools, providing support services (e.g. for children with
special needs), and acting in an advisory role to the head teacher regarding school
performance and implementation of government initiatives. LEAs also have an important role
in the funding allocations of schools. The bulk of schools funding comes from the
dedicated schools grant which is given to LEAs and then distributed according to the LEA's
own funding formula. The funding allocated to the LEA is based on a historically
determined formula which is mainly driven by the numbers of pupils, ‘additional
educational needs’ and local conditions. These local conditions include population
sparsity, measures of deprivation, and wage costs in the area (Roberts and Bolton, 2017).
As well as allocating funding, the LEA also appoints one or two representatives on to a
school's governing body – a group of parents, teachers and community representatives that
provides governance to the school. LEAs typically offer a number of administrative and
management functions including training, personnel and financial services. Up until the
2010/11 school year, the majority of primary aged pupils (67%) attended community schools
in which LEAs are the statutory employer of school staff, owner of the buildings and the
authority that manages student admissions.9 Most other state primary schools are faith
schools (which have greater autonomy from the LEA). Although parents can apply to send
their child to any primary school (i.e. there are no strict catchment areas), popular
schools are often oversubscribed and places are rationed according to a Schools Admissions
Code.10

<hs>  Academy schools</hs>
  ~~~~~~~~~~~~~~~

When a school becomes an academy, it is governed outside the LEA and is overseen and
funded directly by central government. An academy school is run in many ways like a
company, where governors are classed as trustees or directors and the principal/head
teacher is the chief executive. Strong financial management and governance at the level of
the individual academy are very important (National Audit Office, 2012), especially given
that oversight is no longer provided by the LEA. Unlike Community Schools (i.e. most state
primary schools), academies manage their own admissions. While they still have to adhere
to the Schools Admissions Code, they may choose to run their admissions policy differently
than in the past. Although academies are required to teach a broad and balanced
curriculum, including English, maths, science and religious education, they are not
legally required to use the national curriculum. They have the ability to set their own
pay and conditions for staff and more freedom in their hiring decisions (e.g. they may
hire unqualified teachers).11 Although academies are supposed to be funded on an equal
basis with non-academies, they do get extra funds to cover the services that the LEA
provides freely to other state maintained schools12; therefore, they have greater freedom
on how to use the budget allocation. They also have the responsibility of organising
payroll functions, insurance and accountancy functions in-house or by contracting this
out. Academies also have the ability to change the length of the school day and the shape
of the academic year (through term times). In the interests of minimising risk following
the Academies Act of 2010, the Department of Education adopted a phased approach to the
criteria for schools wishing to convert (National Audit Office, 2012), prioritising and
giving a green light in the conversion process to better performing schools. A key
component of this prioritising decision featured the rating in the reports of the Schools
Inspectorate (Ofsted) that visits schools every 3–5 years and rates schools on a four
point scale ranging from ‘outstanding’ to ‘unsatisfactory’. At the time, about 20% of
schools were rated as ‘outstanding’ and 50% as ‘good’. The coalition government initially
prioritised schools rated as outstanding and fast-tracked their applications for
conversion. The first such schools were converted to academy status in September 2010. In
November of the same year, this fast track route was extended to all good schools with
outstanding features. At the same time, recognising the potential for economies of scale,
academies were also encouraged to convert in chains or undertake some post-conversion
collaborative arrangement with other schools. This option was made available for any
school (irrespective of Ofsted grade) if it joined an academy trust with an outstanding
school or an education partner with a strong record of improvement. In April 2011, the
criteria was further widened to include schools that were ‘performing well’, which
included consideration of the last three years' exam results, the latest Ofsted
inspections, and financial management. As shown in Fig. 1, the initial take-up rate for
primary academies in the first possible academic year (2010/11) was modest. This is
unsurprising given the unexpected nature of the announcement, with legislation being
rapidly passed by receiving royal assent in June 2010 and the fact that schools are likely
to take time before making the decision to take on extra responsibilities (especially
given the small size of primary schools in England). However, after that, there was a huge
rise in the number of primary school academies in England between 2010/11 and 2016/17,
with nearly a quarter of the sector being academy schools by 2016/17. Following the way in
which numbers were constructed for Fig. 1, schools are said to convert in a given academic
school year (September to August) if they are running as an academy by December of that
academic year. Thus, for example, a school is classed as converting to academy status in
2014/15 if it converts at some point during the 2014 calendar year. The number of schools
in the sample of converter academies studied in this paper, by year of academy conversion,
is given in Table 1. There are a number of reasons for there being some discrepancy in
numbers between Fig. 1 and Table 1. Firstly, because of the research design that is
adopted, schools are only included in the sample if they have students enrolled in grades
2 and 6 in each academic year between 2006/07 and 2014/15. Secondly, the analysis focusses
only on academies that voluntarily convert to academy status (around 30% of primary
academies are sponsored academies that typically convert as a result of government
intervention). Thirdly, schools that participated in the KS2 strike of 2009/10, and who
therefore have missing outcome data in that year, are excluded. One further institutional
detail of interest is that, in the post-May 2010 phase of academisation, schools have also
been encouraged to convert in a chain or partnership. The Department for Education has
stated ‘this can enable schools to support one another once they are academies, share
resources, experience and ideas. Such an approach is particularly valuable to small
primary schools where working together allows economies of scale to be achieved’
(Department for Education, 2013). The most prevalent model of collaboration is the multi-
academy trust (MAT) wherein all schools within the MAT are governed by one trust and board
of directors. MATs perform a role similar to that which would otherwise be played by the
LEA in that they hire/fire teachers and are responsible for negotiating every aspect of
teacher contracts - the disciplinary process and redundancy pay amongst other things -
with the exception of pensions. MATs can also substitute for local educational authorities
(LEAs) in that they top-slice funds allocated to schools under their trust and use this to
supply central services previously provided by the LEA. In 2016/17, about 80% of primary
academies were in a multi-academy trust. In the sample studied here, there are slightly
fewer schools in MATS, with around 70% operating under this organisational structure.

<hs>  Data</hs>
  ~~~~

The National Pupil Database (NPD) is a census of all pupils in the state system in
England. NPD includes basic demographic details of pupils – such as ethnicity, free school
meal eligibility (FSM), gender, and whether or not English is their first language. The
school attended by pupils can be linked to other school-level information such as the date
of conversion to an academy school and the date and grade of Ofsted inspections (which are
publicly available data). The data is longitudinal and tracks students as they progress
through the state school system. As discussed in Section 2, the national curriculum in
England is organised around Key Stages, the first two undertaken in primary school (in
grades 1 to 6) and the second two in secondary school (in grades 7 to 11). Head teachers
have a statutory duty to ensure that their teachers comply with all aspects of the Key
Stage assessment and reporting arrangements. During primary school, this corresponds to
Key Stage 1 and 2 which respectively cover grades 1–2 and 3–6. Local Authorities (and
other recognised bodies) are responsible for moderation of schools. Thus, although
teachers make their own assessments of students (and therefore could be susceptible to
potential bias), there is a process in place to ensure that there is a meaningful
assessment that is standardised over all of England. At the end of grade 2 in Key Stage 1,
students are given a ‘level’ (i.e. there is no test score as such). However, following
standard practice, National Curriculum levels achieved in Key Stage 1 assessments are
transformed into point scores using Department for Education point scales and these scores
are used in the empirical work reported on below.13 At the end of primary school in grade
6 (or the end of the Key Stage 2 phase of education), pupils take national tests in
reading and maths, which are externally set and marked on a scale of 1–100. The final
dataset used in this paper consists of multiple cross sections of grade 6 pupils linked to
their school, demographic information, and test scores for the academic year 2006/07 to
2014/15. Test scores – both baseline KS1 and the outcome KS2 - are standardised, within
the sample, at the grade/year/subject level. Other data sources are utilised in parts of
the empirical analysis. The School Workforce Census is school level data that is available
from the 2010/11 school year and provides a snapshot of each maintained school's workforce
composition. Also studied is publicly available information on the income and expenditure
of maintained schools and academies that is available from the 2009/10 school year.
Finally, some results from a survey conducted by the Department for Education regarding
the use of academy freedoms are presented (the source of these survey data is Cirin,
2014). This survey, which covers 25% of the 2919 academies that had opened by 1st May
2013, pertains to the freedoms exercised by schools once they gain academy status.

<hs>  Methodology</hs>
  ~~~~~~~~~~~

The main research question of interest is to identify the effect of academy conversion on
pupil achievement in the grade 6 national Key Stage 2 tests taken by pupils at the end of
primary school. Administrative data that follows pupils through their school careers is
used to estimate the impact of academy enrolment on Key Stage 2 performance. In order to
study this, a research design where instrumental variables are combined with difference-
in-differences is implemented. In this design, outcomes of individuals in academies are
compared with those who attend schools that later become academies, but do so after they
sit their KS2 exams. In (1) i denotes pupil, s denotes the legacy enrolment school and t
denotes school calendar year. Thus, αs is a legacy enrolment school fixed effect14 and αt
is a time effect for the academic year in which the pupil is in grade 6. The vector X is a
set of control variables, and the binary Academy variable takes value 1 if pupil i who was
legacy enrolled in school s sits their end of primary school KS2 examination in an academy
school. Finally, v1 is an error term. Despite already restricting to the legacy enrolment
sample so as to avoid endogeneity concerns it may still be problematic to estimate Eq. (1)
by ordinary least squares because legacy enrolled pupils may leave the school before the
end of Key Stage 2. To allow for students to (potentially) sort into schools non-randomly
as a result of the school obtaining academy status, an instrument for academy attendance
is therefore used. This is whether or not the pupil was already enrolled in the school in
the year prior to conversion in grades 2–5. Those for whom this variable takes a value of
one are referred to as being intention-to-treat (ITT). Attention is focussed on those pre-
enrolled in grades 2 to 5 as grade 5 is the penultimate year of primary education and
grade 2 is when the KS1 assessment takes place, thus ensuring that KS1 assessment does not
take place in an academy for the ITT pupils.15 It is important to note that pupils
enrolling in the school after conversion are not included in the analysis. To ensure that
the control group and treatment group are selected in the same way, a slightly different
control group is used for each cohort of academy converters. For those converting in
2010/11 for example, the control group consists of pupils who are in grades 2–5 in 2009/10
at schools that convert between 2011/12 and 2016/17, but are not expected to sit their
exams in an academy.16 Control groups are defined similarly for all schools converting up
to and including 2014/15.17 Because of these restrictions, the event study on pupil
performance has to be limited to a maximum of four years post-conversion, including the
year of conversion itself. This is because there are 4 remaining years of primary school
after the Key Stage 1 assessment. Thus, pupils affected by conversion in grade 2 of
primary school (when KS1 assessments are taken) could have up to four post-conversion
years of education in the academy. Similarly children affected by conversion when enrolled
in the predecessor school in grade 3 could have up to three conversion years, and so on
for children in grades 4 and 5 in the predecessor school. In the first stage, Eq. (2),
estimates of θ2 show the proportion of the ITT group that stay in the academy and take
their KS2 tests there. Eq. (3) is the reduced form regression of KS2 on the instrument. A
two stage least squares estimate (2SLS) estimate can then be obtained as the ratio of the
reduced form coefficient to the first stage coefficient, θ3/θ2. The main specifications
that are estimated - Eqs. (2) and (3) - are based on pooled data for the five cohorts of
academy conversions already described. Extending this to an event study framework enables
separate estimates for the number of years a pupil is exposed to being in an academy post
conversion (up to a maximum of four including conversion year) to be obtained. In this
case, there are four instruments for whether a pupil is expected to sit their exams in the
year of conversion (those in grade 5 in the year prior to conversion to instrument one
year of exposure), the next year (those in grade 4 in the year prior to conversion to
instrument two years of exposure) and so on up to the maximum of four years exposure (for
those legacy enrolled in grade 2). It should be noted that, because of the data that we
have, not all cohorts of converters contribute to the exposure estimates for later years.
For instance, we can only identify the effect of four years exposure for those who are
pre-enrolled in grade 2 in the first two cohorts of conversions.

<hs>  Comparison schools</hs>
  ~~~~~~~~~~~~~~~~~~

A naive comparison between primary academies and all other state-maintained schools is
likely to suffer from significant selection bias, since (as discussed above) conversion to
an academy was done on a voluntary basis and better-performing schools were prioritised
and actively encouraged to convert.18 One might expect schools seeking to become academies
to have common unobservable characteristics such as having a school ethos more in line
with the academy model. To account for this, pupils attending future converters are used
as a control group in a difference-in-differences setting. Thus the data structure that is
utilised is a balanced panel of schools for the school years 2006/07 to 2014/15 with
repeated cross-sections of grade 6 pupils.

<hs>  Balancing tests</hs>
  ~~~~~~~~~~~~~~~

This approach can be legitimised first through covariate balancing tests between treatment
and controls in the baseline academic year (2006/07). Second, and probably more
importantly, the empirical analysis shows there to be no evidence of differential pre-
conversion trends in outcomes between pupils in treatment and control schools. On the
former of these, Table 2 shows the extent to which treatment and control groups are
balanced at baseline (2006/07) for the full sample of treatment and control schools, and
separately for outstanding and non-outstanding schools. In terms of the full sample of
schools, there is a significant difference with respect to KS2 scores prior to the policy,
with treatment schools being better performing in maths. The workforce in treatment
schools also appears to be both larger and, on average, younger and there are more pupils
enrolled in the treatment schools. The above differences are not so surprising when it is
acknowledged that the government prioritised better performing schools for conversion to
academy status. For instance, within the sample of schools studied here, over 80% of the
first cohort of conversions were deemed outstanding by Ofsted. This proportion declines
monotonically to 11% for the 2016/17 cohort of conversions.19 For this reason it is
necessary to look within Ofsted grades (as defined by the latest Ofsted grade awarded
prior to 2010/11) when comparing treatment and control schools. When this is done, the
schools look much more balanced on observables.20 In fact, as Table 2 shows, within
categories of outstanding and non-outstanding schools, there are few statistically
significant differences at baseline between treatment and control schools. In fact, for
outstanding schools there are no statistically significant differences (at the 5% level)
for any baseline characteristics including KS2 and KS1 scores.21 Thus, regressions are
estimated for schools within each Ofsted grade, as well as for the pooled sample.22

<h>DID PRIMARY ACADEMIES CHANGE THEIR MODES OF OPERATION?</h>
------------------------------------------------------

Before looking at the effect of primary academies on pupil performance, evidence is
presented on whether changes in the mode of operation occurred at primary schools that
became academies prior to or during the 2014/15 academic year. Four aspects of this are
considered. First, whether primary schools took up the option to exercise the many academy
freedoms that became available from increased autonomy. Second, whether patterns of
expenditure changed. Third, whether there were changes in workforce composition. Fourth,
whether academies altered their pupil intake.

<hs>  Use of academy freedoms</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

There have been various investigations into whether schools actually use their academy
freedoms upon conversion (e.g. Academies Commission, 2013; Cirin, 2014). The existing
descriptive evidence confirms that they mostly do, but with some degree of variation. The
Academies Commission (2013) conclude that take-up of freedoms had been ‘piecemeal rather
than comprehensive’, in part because changes can take time to implement and sometimes
require consultation. Surveys of recent converters by Bassett et al. (2012) and Cirin
(2014) found financial motives to be important in the decision to convert. In the former
study, over 75% of respondents cited it as one of their reasons for converting and two-
fifths as their primary reason. Cirin (2014) found that the desire ‘to gain greater
freedom to use funding as you see fit’ was the most commonly cited reason for conversion
(cited by 83% of respondents). The vast majority (almost 9 in 10) also moved to procure
services themselves. Importantly, Cirin (2014) breaks down results by primary and
secondary status. This shows that the majority of academies do exercise freedoms, but this
is more common in secondary than in primary schools. This is shown in Table 3, taken from
his survey of 720 academies which were open on 1 May 2013. The numbers in the Table show
that most schools report a use of academy freedoms, but that the percentage of primary
schools making a particular change is smaller than it is for secondary schools.
Furthermore, Cirin (2014) reports that almost all schools surveyed made at least one
change (702 out of 720), implying that at least 95% of primary converters (262 primary
converters were surveyed) exercised at least one freedom, with two-thirds believing that
the changes improved attainment.

<hs>  Changes in expenditure patterns</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Studies cited above on the use of academy freedoms suggest that the financial motive to
convert was important. Table 4 shows numbers on income and expenditure before and after
conversion in treatment and control schools using administrative data on school income and
expenditure. Changes between the 2009/10 and the 2014/15 school years are reported. There
are some data issues that need to be highlighted upfront before discussing these numbers.
First, the timing of reporting changed after conversion, with academies reporting in the
September–August school year as opposed to the April–March financial year.23 The latter is
in line with local authority financial statements and was the practice in schools before
they converted to become an academy and in control schools throughout the period of the
analysis. Secondly, accounts for schools that do not convert in the period (the control
schools) do not include the value of LEA provided services; however, information is
available on how much extra income is given to academies to cover the value of these
services (the Education Services Grant - ESG). To make the numbers comparable this is
removed from both the grant income and expenditure for academies in column (2) of Table 4.
Columns (1) and (4) of Table 4 show that per pupil income and expenditure was similar for
the treatment and control schools before conversion. For example, as shown in Panel A,
total income in all treatment and control schools was £3974 and £4156 per pupil
respectively. Total expenditure was £3966 and £4154 per pupil in treatment and control
schools respectively. As shown in Panels B to C of the Table, these pre-conversion numbers
are also closely aligned for the comparisons undertaken within the outstanding and non-
outstanding groups of schools. It is evident, however, that converting primary schools
both received more money and spent more money post-conversion, even once the extra money
given for LEA provided services is accounted for. The Table also shows the income and
expenditure per pupil after conversion and a difference-in-difference estimate in the
final column. This shows significant income and expenditure gaps arising after conversion
relative to what happened in the control schools. The differences in total income and
expenditure are estimated as £296 and £522 per pupil per year. The increases are clearly
driven by the relative increase in grant income. A similar qualitative pattern is shown
for schools classified as outstanding and non-outstanding, but with higher income and
expenditure shown for the latter schools, most likely reflecting a higher proportion of
disadvantaged students in this group. Table 5 shows the change in categories of
expenditure per pupil before and after conversion.24 There are three Panels, which differ
according to assumptions made about which services the academies procure post-conversion
given that they are no longer provided for them by the local authority. The numbers in the
upper Panel A are changes inclusive of the extra money delegated to them. The numbers in
the middle Panel B subtract an equal share of the ESG money from each category of
expenditure. Finally, those in the lower Panel C remove all of the extra ESG money from
the expenditure on non-staff related running costs. In each case it is very clear that,
even though primary academies spent more on teaching staff, non-teaching staff, and other
running costs after conversion (relative to control schools), the increase was greater for
administrative costs (i.e. non-teaching staff and other running costs). This is true for
schools in all Ofsted categories. Because the amount of money earmarked for services
previously provided by LEAs from expenditure is removed, these shifts cannot be attributed
solely to the mechanical shift caused by the school having to take on more administrative
tasks post-conversion. It seems that the primary academies studied in this paper did
receive more income, but that they spent it disproportionately on day-to-day running
operations rather than on ‘frontline services’ such as teaching staff.

<hs>  Changes in workforce</hs>
  ~~~~~~~~~~~~~~~~~~~~

Table 6 reports evidence on changes in the composition of the school workforce between
2010/11 and 2014/15 for schools that became academies in that period relative to schools
that became academies in 2015/16 and 2016/17. Changes are shown for all schools and
stratified by Ofsted rating. The Table reports difference-in-differences estimates for the
total number of teachers employed, the pupil/teacher ratio, the mean teacher salary, the
proportion of teachers who are in the leadership group or whether the school changes its
head teacher. In general, the results reported in the Table show little evidence of
workforce changes resulting from academisation. The one exception is head teacher
turnover. For the full sample, there is a statistically significant 6.3 percentage point
reduction in head teacher turnover in primaries that became academies. When broken down by
Ofsted category, this occurs only in non-outstanding schools, which are 7.2 percentage
points less likely to take on a new head teacher. This stands in direct contrast to the
finding of Eyles and Machin (2015) who found that the vast majority of the first phase of
academy conversions in the 2000s were characterised by new head teachers coming into
academies and therefore that changes in managerial structure were a key feature of academy
conversion that facilitated increased autonomy. This mechanism appears to be completely
absent in the case of primary schools.

<hs>  Changes in intake</hs>
  ~~~~~~~~~~~~~~~~~

Alongside performance effects we look at whether pupil composition changed once a school
gained academy status. As data is available prior to 2010/11, the analysis considers year-
on-year changes between 2006/07 and 2014/15 in the characteristics of those entering the
earliest grade in which the schools enrol pupils. We also include observations of pupils
over this period that enter schools which become academies after the sample ends (in
2015/16 and 2016/17). The three outcomes considered are the fraction of the pupil intake
who are eligible for free school meals, the fraction with English as a native language,
and the total size of the entry year intake (in logs). In each case, school and year
effects are included. The results, presented in Table 7, show no evidence that schools
alter their intake along these dimensions.25

<h>SUMMARY</h>
-------

Taken together, the findings show that primary schools changed some aspects of their
operations after becoming academies. In particular, most primary academies began to use
freedoms made available to them as a consequence of conversion. They also received more
income and altered how their expenditure was allocated across functions. With regard to
the latter, the observed spending changes mainly affected administrative functioning and
day-to-day operations, because of the removal of such provision from the local authority.
At the same time, there was not much change in the school personnel or in composition of
the pupil intake.

<h>5. PUPIL PERFORMANCE RESULTS</h>
----------------------------

This section reports the results on pupil performance, starting with the main baseline set
of results showing the causal impact of academy conversion on pupil performance. Then, in
the light of the previous section's results showing that most, but not all, primary
schools altered their modes of operation post-conversion, heterogeneous estimates along a
number of dimensions are reported.

<hs>  Main results</hs>
  ~~~~~~~~~~~~

Table 8 shows estimates of the 2SLS specifications studying the impact of academisation on
pupil performance in reading and maths tests at the end of primary school. Separate
coefficients are shown for each subject, both for the pooled sample and by whether the
predecessor school's Ofsted grade was outstanding or not. Columns (1) to (3) show
estimates when the treatment is whether the school converts to academy status. Columns (4)
to (6) show estimates for years of exposure. As the vast majority of legacy enrolled
pupils stay in the school to take their KS2 exams - first stage estimates range from 0.92
to 0.95 - only 2SLS estimates are presented. In all cases, there is no evidence of any
performance boost from academisation. The estimates are small in magnitude, sometimes
negative, and almost all statistically insignificant. In terms of magnitude, the largest
positive estimate is 0.02σ (with standard error 0.03) for reading in outstanding schools
as reported in specification (2) of the Table. All of the other 2SLS estimates are lower
than this, and nine of the twelve maths and reading estimates (including all six for
maths) have negative signs. When considering the average of reading and maths scores it
seems that primary age pupils did not benefit from attending an academy school in terms of
their performance at the end of primary school.26 As results prove similar whether reading
or math marks are used as the outcome of interest, only results based on average points
are shown for the rest of the paper.27 One might be concerned about the research design
being potentially contaminated by differential pre-policy trends.28 Fig. 2 therefore shows
estimates from an event study, for the pooled sample, for pupils attending academies four
years prior to academy conversion to three years after. The effects of being in an academy
remain numerically small and insignificant (as the c to c + 3 coefficients all overlap
with the zero line on the Figure). Moreover, there is no sign of pre-policy trends, nor
any gradual improvement in results post-conversion. Table 9 also further generalises the
Table 8 baseline results by reporting estimates for legacy enrolled pupils by discrete
years of exposure, ranging from one to a maximum of four. Again, there is neither any sign
of a positive effect nor any suggestion that benefits might be increasing with years of
exposure. If anything, the opposite is the case, as the absolute values of the negative
coefficients mostly get larger with more years of exposure.

<hs>  Heterogeneity</hs>
  ~~~~~~~~~~~~~

While there is no evidence of performance effects on average, both in the event study and
years of exposure analysis, it may still be the case that academisation has scope to
benefit some subsets of students and not others. It is also possible that certain school
characteristics may be associated with differential academy effects on pupil performance.
Table 10 therefore shows results from an investigation of whether the estimated 2SLS
effect size differs in several ways: i) with whether the pupil is eligible for free school
meals or not; ii) with an indicator for whether the school is in an urban area or not
(given that the charter school literature finds positive effects to be concentrated
amongst urban schools); iii) whether it differs with pre-conversion school size (as larger
schools may be more adept at managing their extra freedoms); and iv) whether the school
joins a multi-academy trust (MAT). The results reported in the Table do little to alter
the prior analysis. First, there is little evidence that the effect of academy attendance
differs depending on whether one is eligible for free school meals or attends an urban
academy. Panel C of Table 10, shows that the same can be said for pupils attending schools
of differing sizes. Although performance effects appear to decline with school size, none
of these interactions reach statistical significance. The final aspect of heterogeneity
considered – whether or not pupils attend an academy that becomes part of a (MAT) or not –
does uncover some differences. The most noteworthy is that some of the estimates for not
being in a MAT are significantly negative. This is the case for all schools where there is
a 0.06σ (0.02) fall – closer investigation shows that this is confined to the non-
outstanding schools. This is consistent with the hypothesis that conversion in stand-alone
(non-MAT) schools, which are not able to benefit from the economies of scale that a MAT
can bring, may have actually proven detrimental to pupils enrolled in previously non-
outstanding academies. However, this result should be taken with caution. About 60% of the
primary academies considered here are part of a MAT, but it should be acknowledged that
whether or not a school is able to join a trust is endogenous to KS2 performance; results
showing performance drops could be due to negative selection to the category of non-MAT
academy schools (evident only for non-outstanding schools).

<h>CONCLUSION</h>
----------

The English government has radically restructured its school system under the assumption
that academisation delivers benefits to schools and students. This paper studies the
unexpected policy change that occurred in 2010 that enabled (and encouraged) primary
schools to become academies. It looks at the first primary schools that have become
academies in England (between 2010/11 and 2014/15) and finds no evidence of pupil
performance improvement resulting from conversion. How should an overall zero effect be
interpreted in the light of evidence showing positive effects of autonomy in other
contexts? One reason is that schools that converted were already doing well within the
system and simply did not require additional autonomy in order to thrive and therefore did
not make substantive changes. Indeed the limited changes that are seen – increasing
expenditure on non-instructional tasks – do not correspond to the kinds of changes, such
as effective discipline and higher quality teaching that have been found to increase test
scores in other contexts such as charter schools (Fryer, 2014). In existing research, much
of the positive effects of autonomous schools have been shown for disadvantaged students
and not so much for advantaged students. While there was scope to improve achievement
within these schools, it may be that changes introduced as a result of school autonomy
simply do not benefit such students at the margin. However, given the survey evidence
reported above and the research into how additional income was used by schools, it would
appear that many of these schools did not make changes that affect ‘frontline services’
(as opposed to administrative roles). Another possible reason is that effects are
estimated in the short run. It may be that the programme will bear fruit once more schools
convert and facilitate greater economies of scale by entering into or deepening
collaborative arrangements with each other. In the heterogeneity analysis, we found some
evidence of variation by whether or not schools are in a multi-academy trust. Although we
do not take the effect to be causal due to the endogenous decision to join a MAT, it is
still a worrying finding that performance dips for the non-outstanding primary schools
(around 40% of converters) that do not join a multi-academy trust. Finally, one of the key
models for some successful urban charters in the US and some secondary schools in
England29 – an effective discipline approach for academies and the No Excuses model of
charters – is of less relevance to the age range of children enrolled in English primary
schools than for secondary age children (since behavioural problems that may lead pupils
to be suspended or excluded from school are much more prevalent in the latter).30 In the
light of all these factors, it is not surprising that there has been no overall effect on
pupil performance. One might argue that if academisation has no average effect on pupil
performance, this could still be a reasonable public policy if there are other reasons for
why this might be beneficial – for example, if school leaders can more easily make changes
that might benefit students (or their parents) and staff. However, the process of
restructuring individual schools has been shown to be financially costly and restructuring
on a system wide basis would likely prove to be too costly in the long run if it fails to
generate gains for students in terms of test scores. Furthermore, risks are also posed by
an increasing number of schools becoming academies.31 For example, they are no longer
regularly monitored at the local level. Problems might not therefore come to light unless
they are flagged up by an Ofsted inspection, which are not regular events. There are
potential negative spill-overs on other schools if opting out of Local Authority control
undermines services that the Local Authority is able to provide to other schools in the
same geographic area (e.g. child psychologists to support children with special needs in
many schools). Studying the operational aspects of academies, and the institutional
structures in which they function, is an important subject for future research.


<h>REFERENCES</h>
----------

  [1] Atila Abdulkadiroǧlu, Joshua D. Angrist, Peter D. Hull, Parag A. Pathak. Charters without lotteries: Testing takeovers in New Orleans and Boston. doi:10.1257/aer.20150479
  [5] Anders Böhlmark, Mikael Lindahl. Independent Schools and Long-run Educational Outcomes: Evidence from Sweden's Large-scale Voucher Reform. doi:10.1111/ecca.12130
  [7] Damon Clark. The performance and competitive effects of school autonomy. doi:10.1086/605604
  [10] Andrew Eyles, Claudia Hupkau, Stephen Machin. Academies, charter and free schools: Do new school types deliver better outcomes?. doi:10.1093/epolic/eiw006
  [11] Andrew Eyles, Claudia Hupkau, Stephen Machin. School reforms and pupil performance. doi:10.1016/j.labeco.2016.05.004
  [12] Roland G. Fryer. Injecting charter school best practices into traditional public schools: Evidence from field experiments. doi:10.1093/qje/qju011
  [13] Eric A. Hanushek, Ludger Woessmann. The Economics of International Differences in Educational Achievement. doi:10.1016/B978-0-444-53429-3.00002-8
<ART>Voting suffrage and the political budget cycle: Evidence from the London Metropolitan Boroughs 1902-1937
================================================================================

Authors: Toke S. Aidt, Graham Mooney
DOI: 10.1016/j.jpubeco.2014.01.003
Year: 2014  |  Pages: 53-71
ASJC codes: 2002, 2003
Keywords: Local public finance, London, Opportunistic political budget cycles, Suffrage, Voting franchise

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We study the opportunistic political budget cycle in the London Metropolitan Boroughs between 1902 and 1937 under two different suffrage regimes: taxpayer suffrage (1902-1914) and universal suffrage (1921-1937). We argue and find supporting evidence that the political budget cycle operates differently under the two types of suffrage. Taxpayer suffrage, where the right to vote and the obligation to pay local taxes are linked, encourages demands for retrenchment and the political budget cycle manifests itself in election year tax cuts and savings on administration costs. Universal suffrage, where all adult residents can vote irrespective of their taxpayer status, creates demands for productive public services and the political budget cycle manifests itself in election year hikes in capital spending and a reduction in current spending. © 2014 The Author.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Suffrage rules regulate who can vote and this, in turn, influences the interests served by
elected politicians. While today we associate democracy with equal and universal suffrage,
historically the power to elect or appoint representatives was the privilege of narrow
elites. Suffrage rules focussed on specific characteristics of the individual such as
ownership of property, payment of taxes, residency and gender. The logic behind linking
the right to vote to property holdings or tax payments can be traced back to mediaeval
Britain and reflected the belief that it restricted the franchise to individuals with a
longer-term interest in the welfare of the community, akin to the shareholders of
corporations. Economic models in the tradition of Meltzer and Richard (1981) predict a
straightforward positive link between demands for public goods and redistribution and
extension of the franchise. However, evidence from analyses of historical data show that
the impacts were more complex than predicted by theory and were functions of the specific
rules that determined who could vote.2 While progress has been made in understanding the
public finance consequences of franchise extension, little is known about the influence
these rules have on the incentive to manipulate tax and spending patterns prior to
elections in the quest for votes. A well-established literature, drawing on evidence from
modern democracies and surveyed by Paldam (1997), Alesina et al. (1997) and most recently
by Drazen (2008), offers a strong argument for the existence of opportunistic political
budget cycles in both national and local elections.3 The construction of cross-country
datasets (of OECD countries and more recently of developing countries) and of rich
datasets for local governments (municipalities or states) from the modern period has
tended to draw attention to the experience of the late 20th and early 21st centuries at
the expense of earlier periods. Consequently the focus has been on opportunistic political
budget cycles operating under universal suffrage; quite how the cycle might manifest
itself in polities with economic and social restrictions on who could vote has been
completely overlooked. The purpose of this paper is to draw upon the historical experience
of early 20th century London to study the nature of the political budget cycle under two
different suffrage regimes: taxpayer suffrage, where the right to vote is linked to
specific tax payments; and universal suffrage, where all adults can vote (with minor
qualifications), irrespective of their economic status. While the identity of the “pivotal
voter” differs systematically under the two suffrage rules, electorally-motivated
politicians can be expected to be equally determined to manipulate fiscal policy before
elections to win support from the pivotal voter. We, therefore, conjecture that an
opportunistic political budget cycle will be present in both regimes but that its nature
will vary systematically with the suffrage rules.4 The setting for our study is the London
Metropolitan Boroughs (LMBs) before and after the First World War. The 28 LMBs were
established in 1899 and had powers to levy local property taxes, to decide on the
provision of local services (sewer connections, bathhouses, parks, libraries, dairies and
milk shops, etc.) and to take out loans to finance capital expenses on the security of
future property taxes. Within the statutory boundaries, the LMBs had significant fiscal
autonomy and the elected representatives of the councils could decide on the level,
composition and the timing of key fiscal variables. All councillors were elected every
three years. The franchise before the First World War was based on property tax payment
and restricted to men; we refer to it as taxpayer suffrage. The Representation of the
People Act (sometimes referred to as the Fourth Reform Act) in 1918 eradicated the tax
payment requirement at all levels of government (including for the LMBs) and introduced
almost equal and universal suffrage.5 This quasi-natural experiment allows us to study the
opportunistic political budget cycle under two different suffrage regimes.6 Besides adding
new historical evidence to the debate on the opportunistic political budget cycle, our
study contributes directly to two more specific strands of literature.7 Firstly, it
significantly enhances our understanding of fiscal retrenchment and taxpayer democracy in
Britain. Until 1918, voting rights in local elections linked representation to the prompt
payment of the local property tax (known in Britain as the rate) such that only local
taxpayers had the right to vote. This had intriguing implications for the relationship
between the size of the electorate and local public finance. In particular when the
balance of power shifted to small-scale, middle class taxpayer-voters, demands were made
for retrenchment and economy rather than fiscal expansion, despite apparently large social
returns on public investment in local public goods (Hennock, 1963, 1973; Wohl, 1983;
Szreter, 1988, 1997). As documented by Aidt et al. (2010), this generated a negative
relationship between spending on local public goods and the extension of the franchise.8
We add to this by studying how opportunistic political budget cycles operate in an
environment with taxpayer-voters. This restricted franchise is compared to the regime of
universal suffrage, where the pivotal voter often does not contribute much to the local
tax base. Secondly, our study contributes to the fast expanding research on the
conditional political budget cycle initiated by Persson and Tabellini (2003), Brender and
Drazen (2005), Shi and Svensson (2006), Alt and Lassen (2006a,b) and Alt and Rose (2007)
amongst others, and recently surveyed by de Haan and Klomp (2013). The general point here
is that the size and nature of the political budget cycle are conditional on the political
and economic environment. They depend, amongst other factors, on economic conditions
(e.g., the level of income), the institutional framework (e.g., the level of corruption,
the type of election or political system), and the monitoring framework (e.g., fiscal
transparency and quality of the press). We add an important dimension to this
conditionality by showing that the opportunistic political budget cycle is influenced by
the details of the franchise. We find the following results. Under taxpayer suffrage
(1902–1914), the opportunistic political budget cycle materializes as tax cuts and in
reduced spending on administration in election years. Under universal suffrage
(1921–1937), we find that expenditures in election years are shifted towards productive
public goods (capital spending) and away from other types of (current) spending, with no
effect on tax income. The LMBs operated under a balanced budget rule which limited their
ability to deficit finance election year tax cuts or spending booms, yet we find evidence
of smaller surpluses in election years under both suffrage regimes. We interpret these
findings in the light of the different incentives that variations in the suffrage rules
generate for politicians to engineer opportunistic cycles. Building on Lohmann (1998), Shi
and Svensson (2006), and Aidt et al. (2010), we provide a formal rational choice model
that illustrates the logic. Under a restricted taxpayer suffrage that explicitly
disenfranchises non-taxpayers and enfranchises owners of property in the locality who can
reside elsewhere, taxpayer-voters often demand retrenchment and economy. Politicians
respond to this by cutting taxes and reducing spending on administration in election
years, as we observe in the data. In contrast, under universal suffrage all adult
residents hold the right to vote, including many poorer residents who contribute little in
terms of property tax payments to the funding of spending. This generates demand for
fiscal expansion. Politicians, therefore, aim to engineer additional electoral support by
adjusting the portfolio of spending towards productive public services which benefit the
pivotal voter and away from other spending without necessarily increasing taxes. The rest
of the paper is organized as follows. In Section 2, we introduce the institutional setting
of our study and the particularities of the suffrage rules governing elections to the
councils of the LMBs before and after the First World War. In Section 3, we develop the
theoretical foundation for our empirical investigation. To this end, we sketch a rational
choice model and provide an online supplementary appendix with technical details. In
Section 4, we present the data and discuss some stylized facts about local public finance
in London between 1902 and 1937. In Section 5, we consider the evidence of an
opportunistic political budget cycle. In Section 6, we lay out our empirical strategy. We
present the main findings in Section 7 and in Section 8 we discuss alternative
interpretations and robustness checks. The concluding remarks in Section 9 recapitulate
our findings in the context of conditional political budget cycles.

<h>THE INSTITUTIONAL SETTING</h>
-------------------------

The 28 LMBs were established by the London Government Act of 1899 and they took office in
November 1900 (Robson, 1939, chapter 10; Young and Garside, 1982).9 LMBs were created from
the largest of the existing Vestries and District Boards of Works and by combining smaller
Vestries and Boards into bigger and fiscally more viable units.10 As with the Vestries and
District Boards, the main responsibility of the boroughs was the provision of local urban
amenities. This included construction and maintenance of local streets, refuse collection,
provision of public lighting (by 1912, 15 LMBs were generating their own electricity for
street lighting), sewers and drainage, burial grounds, libraries, parks, baths and
washhouses, and the employment of health officers. They could also purchase land and build
public sector housing (White, 2001). Other services, such as schools, infectious disease
hospitals, policing and major roads and infrastructure projects fell outside their
jurisdiction and were handled by a variety of city-wide authorities, but the bulk of
spending on sanitation and health-related public services was undertaken by the
boroughs.11 The responsibilities stayed constant over the period from 1901 to 1937 (in
fact to the 1960s) and there were no substantial changes in fiscal federalism over the
period.12 The main source of LMB revenue was receipts from the rate – the local property
tax – which often contributed around 90% of total income. User charges for specific
services were also important and some equalization funds were available, though poorer
boroughs complained about the iniquity of the redistribution (Booth, 2009). From this
base, the boroughs provided local public goods and financed the administrative cost of
running the council. They also collected taxes on behalf of other local authorities (e.g.,
the School Board for London, London County Council, the Boards of Guardians, and the
Metropolitan Police). Within these institutional and fiscal constraints, the elected
councillors had freedom to allocate public monies as they saw fit and to raise the tax
resources they deemed necessary to fund required expenditures. While they could borrow
funds for the purpose of capital investment, they were not allowed to do so to finance
current spending and they effectively operated under a balanced budget rule which,
however, did not preclude surpluses. The LMBs were governed by a council, consisting of a
mayor, aldermen and councillors.13 These were elected in competitive elections. Unlike
prior to 1901, where elections for the Vestries took place each year for a third of the
vestrymen, all the LMBs adopted an election cycle in which the entire council was elected
every three years.14 The rules governing the electoral franchise for the LMBs between 1901
and 1918 were codified in the Local Government Act of 1894. Voters consisted of two groups
of men (and a limited number of widows and spinsters): the Parochial Electors and the
Parliamentary Electors were entitled to vote under the Parliamentary Reform Act of 1884
and the Registration Act of 1885 (Keith-Lucas, 1952, p. 233). Both groups were required to
occupy a property in the borough for a sufficient time period (ranging from 6 to 12
months), but permanent residence in the borough was not necessary. Some boroughs,
therefore, had a significant number of absentee voters. Most importantly, however,
eligibility to vote for the council was linked directly to payment of the rate. Provided
that the occupancy requirement was satisfied, the right to vote was conferred on occupiers
of property worth at least £10 and had been subject to 12 months' rating with the rate
paid in full. This implied that the right to vote was restricted to the taxpayers of the
borough who had paid their dues on time and in full. This disenfranchised many poorer
inhabitants. Since the fraction of the total stock of property rated in each borough
varied (slum areas were sometimes not rated) as did the diligence of tax collection, the
fraction of males aged 20 and above that could vote varied greatly. In 1909, for example,
about 37% of adult males in Stepney and 78% of adult males in Battersea were eligible.15
The average extension of the franchise across the boroughs between 1902 and 1914 was about
60%. We refer to this as the taxpayer suffrage. Taxpayer suffrage was abolished by the
Representation of the People Act of 1918 which established one standard franchise for all
general and local elections in Great Britain. For men the requirement was six months'
occupation of land or premises in the area (i.e., no tax payment requirement). The
condition for women was six months' occupation of land or premises in the area or as the
wife of a man so qualified, on account of premises in which they both resided, if she was
30 years old (Keith-Lucas, 1952, p. 235). The Act also abolished the disenfranchisement of
paupers for all local government purposes. While owners of land or buildings within the
borough previously were entitled to vote whether they lived in the borough or not, after
1918 they qualified to be elected as a borough councillor, but not to vote. Although some
women had to wait until 1928 to get the right to vote, we refer to this post-1918
situation as universal suffrage.

<h>THE BUDGET CYCLE AND THE SUFFRAGE: A THEORETICAL FRAMEWORK</h>
----------------------------------------------------------

We consider a borough populated by capitalists (C) and workers (L) during two periods, t =
1,2. Each capitalist is endowed with capital (k) and two units of housing. Workers are
endowed with one unit of labour, which is supplied in-elastically to a competitive labour
market, and nothing else. There are nc capitalists and more workers than that. Each
period, the capitalists combine their capital endowment with hired labour to produce
output using a CRTS technology. The market clearing wage and profit income, wt⁎ and πt⁎,
are both strictly increasing in total factor productivity. The capitalists “consume” one
unit of housing privately and pay the property tax levied on it directly. The other unit
is supplied to a competitive market as rental accommodation for workers. Under the
assumption that the supply of houses is fixed, the incidence of the property tax levied on
rented accommodation, if any, falls on the capitalists and workers therefore do not pay
the local property tax. The capitalist-politician generates a rational political budget
cycle. The capitalist-politician wants more rents and more spending on the non-productive
public good than do capitalist-voters. Under taxpayer suffrage, the capitalist-politician
cuts spending on the non-productive public good and rents to convince capitalist-voters of
his quality. Since all capitalists agree on the optimal level of the productive public
good, there is no pre-election distortion in that item. The combined consequence is that
the tax rate falls. In short, the rational political budget cycle manifests itself as pre-
election cuts in rents, less spending on non-productive public goods and lower taxes. We
call this the retrenchment hypothesis. Under universal suffrage, worker-voters want more
spending on the productive public good than the capitalist-politician. They are not
concerned with the other budget items because the incidence of the property tax is passed
on and because they do not benefit from non-productive public goods. Consequently, the
capitalist-politician delivers the utility target UUS by spending more on the productive
public good. The maximum rent is then extracted and spending on the non-productive public
good is cut. The reason for the latter is that the increase in spending on g decreases net
profit income, making it optimal to reduce spending on q. The net effect on the tax rate
is ambiguous. In short, under universal suffrage the rational political budget cycle
manifests itself as a pre-election hike in spending on productive public goods and a cut
in non-productive services, with an uncertain effect on taxes. We call this the
expenditure switching hypothesis. The LMBs could not run deficits but surpluses could be
accumulated for precautionary reasons.18 We can capture this by assuming that the
incumbent politician has a surplus target in non-election years but may deviate from this
in election years (at a cost). Under taxpayer suffrage, the benefit is that more rents can
be retained. Under universal suffrage, some of the increase in spending on productive
public goods can be financed by suspending the surplus target. Surpluses may, therefore,
be lower in election than in non-election years irrespective of the suffrage rules. This
is the third hypothesis we test.

<h>DATA</h>
----

Table 1 lists the 28 London Metropolitan Boroughs and the ID number used to identify each
of them in the maps shown below. Information on the LMBs' accounts is published in the
Local Taxation Returns (1901–1914) and in the Local Government Financial Statistics
(1920–1938). These sources contain detailed information on income, expenditures (current
and capital) and debt for each borough. The format of the accounts, however, changed
significantly after the First World War, when the responsibility for collecting and
reporting local government public finance data moved from the Local Government Board to
the Ministry of Health. After this change, a greater emphasis was put on recording
information related to public health. This makes it impossible to match disaggregated
budget items between the two sources and we consider two separate samples, corresponding
to the two suffrage regimes. We stress, however, that a careful reading of the notes to
the accounts gives us no reason to believe that there were any substantial alterations to
LMB accounting practises that could account for systematic differences in the nature of
the political budget cycle before and after the change in suffrage rules. The fiscal year
runs from April 1 to March 31 throughout and we use the convention to refer to a fiscal
year by the calendar year in which it ends. The taxpayer suffrage sample runs from 1902 to
1914. We cannot use the data for 1901 because the accounts only refer to a part of the
year (November 1900 to March 1901) and 1914 is the last fiscal year available since
systematic reporting was suspended during much of the War. The first accounts after the
War for the fiscal year 1920 were incomplete and are excluded from the analysis. The
universal suffrage sample, therefore, starts with the fiscal year ending in 1921 and runs
to 1937. This gives a total of 364 observations for the taxpayer suffrage sample and 476
for the universal suffrage sample.19 The fiscal data is converted into real values using
the Sauerbeck-Statisk price index from Mitchell (1988) with base year 1871 and expressed
in per 1000 capita terms. The seven particular fiscal outcomes that we study are listed
and defined in Table 2. Elections took place every three years: 1900, 1903, 1906, 1909 and
1912 before the War; and 1919, 1922, 1925, 1928, 1931, 1934, and 1937 after. The potential
manipulation of the budget would occur before the election and would therefore fall in the
fiscal year spanning the November election. We define the dummy variable election as being
equal to one if fiscal year t is an election year and zero otherwise. Table 3 reports
descriptive statistics separately for the two samples and Figs. 1–6 show the average
trends for the fiscal outcome variables for the fiscal years 1902–14 and 1921–37,
respectively. We notice a number of important facts. First, both current income and
current expenditure increase in real terms from around £15 per 1000 capita (in 1871
prices) under taxpayer suffrage to £25 per 1000 capita under universal suffrage (see Table
3). The increase in capital expenditure (and capital income) is less pronounced. Secondly,
there were no particular trends in current expenditure or in spending on administration
under taxpayer suffrage (Fig. 1). Likewise, current income and rate income are stable in
this period (Fig. 2). A similar characterization applies to the trends under universal
suffrage (Figs. 4 and 5) and we note that, on average, the LMBs' spending and taxation
levels were comparable in 1914 and 1921, despite the interruption of the War and the
franchise change. We do, however, observe a decline in capital expenditure (and capital
income) under taxpayer suffrage in the years before the War (Figs. 1 and 2). The spike in
capital expenditure in 1905 is entirely attributed to a large investment in electricity in
St. Marylebone and is (more than) matched by a large increase in capital income (a big
loan). Thirdly, around 1930, a marked level shift upwards in current expenditure and in
rate income but not in capital expenditure, takes place. A disaggregated analysis of the
data [not reported] suggests that this reflects increases in spending on streets as well
as increases in wage costs. Gillespie (1989) documents how some boroughs in the 1920s used
resources for public relief work and we conjecture that this endeavour was intensified
during the recession years. Fourthly, we observe substantial year-on-year variation in the
average current deficit (Figs. 3 and 6). Mostly the LMBs were close to balancing the books
and, on average, they ran a small surplus both before and after the change in the
franchise (see Table 3). This suggests that the balanced budget rule mattered, but, at the
same time, allowed some flexibility for fiscal manipulations. The average trends hide
substantial cross sectional variation: some boroughs spent, taxed and borrowed much more
than others. The dispersion is particularly large with regard to capital expenditures (and
income) where the standard deviation is about twice as large as the mean values (see Table
3). We visualize this dispersion in Maps 1–3. Each map consists of two panels, one for the
pre-war and for the post-war period, and colour codes the spatial distribution of rate
income (Map 1), current expenditure (Map 2) and capital expenditure (Map 3). There is a
consistent spatial pattern of high-tax–high-current-spending in north-west London,
including Westminster, Holborn, St. Marylebone, and Hampstead, and Woolwich in the south-
east. These are also the areas with high levels of capital expenditure under taxpayer
suffrage. After the change to universal suffrage in 1918 there is a marked shift in
capital expenditure to the east and south-east of London, with Poplar, Bermondsey and
Greenwich standing out as big spenders. Much political debate was generated after the
First World War about the high-rating and -spending policies of east end Labour councils
such as Poplar. Leaders of the Labour Party in London were worried that this approach
would alienate potential middle-class support in other parts of the capital (Gillespie,
1989). We also collect demographic data – total population, population growth (absolute
change in number of inhabitants), population density (inhabitants per house) and age
structure (proportion of the population below 20) – from the decennial Censuses.20 We do
not have income or GDP data for the boroughs, but we record the average value of
properties subject to taxation in each borough each year and use the variable wealth
(defined as taxable value per 1000 houses) to proxy for income or wealth effects.21 We
record information on the stock of outstanding loans at the end of each fiscal year and
use the variable debt (defined as outstanding real debt per capita), as a proxy for
accumulated spending on public services. Finally, for the taxpayer suffrage sample, we
have collected information on the number of registered voters in each borough. We
normalize this with the size of the adult male population to get the variable franchise
extension which we use to control for variations in the size of the electorate. We have
collected a number of additional variables used for robustness checks. We introduce these
in Section 8.

<h>EVIDENCE FOR THE POLITICAL BUDGET CYCLE</h>
---------------------------------------

The fiscal outcome variables defined in Table 2 are selected to facilitate tests of the
retrenchment and expenditure switching hypotheses. Retrenchment effects would primarily
show up as election year tax cuts. This is captured by rate income and current income
where the latter, in addition to property tax revenue, includes income from user charges
for local public services, but excludes revenues raised on behalf of other local
authorities. Expenditure switching involves increasing spending on productive public goods
that benefits all and cuts in non-productive spending. We presume that the outputs
generated by capital expenditures represent productive public spending. In contrast, many
current spending items are non-productive. Therefore, we use the variables capital
expenditure and current expenditure to test the expenditure switching hypothesis. In
addition, we use the variable capital income to test if there is a tendency to take out
loans in election years. If this is the case, the need to increase the yield from property
taxes to fund the pre-election spending hike in capital spending anticipated under
universal suffrage would be reduced and we might expect to see a fall in tax income to
match the expected fall in current spending. We use expenditure on administration as a
proxy for bureaucratic spending with the rationale that the taxpayer-voter might find such
outlays particularly wasteful.22 Finally, we use current deficit, defined as total current
expenditure minus current income, to test election cycles in the fiscal balance. Before we
turn to the formal statistical analysis, we present some descriptive evidence on the
nature of the opportunistic political budget cycle in London between 1902 and 1937. Figs.
7–10 show plots of the seven fiscal outcome variables in “event time”. That is, each
figure shows the average of the relevant fiscal outcome in election years, one year before
an election and one year after an election. A “V” or an inverted “V” shape indicates a
political budget cycle. We observe a clear revenue pattern under taxpayer suffrage: lower
current income and lower rate income in election years than in other years (Fig. 7). We
note a fall in spending for both administration and current expenditure (Fig. 8). The
pattern is noticeably different under universal suffrage (Figs. 9 and 10). The budget
cycle in rate income has gone. Instead, we observe a clear election year increase in
capital expenditure with a hint of a cycle in current income. Under both franchise
regimes, surpluses are lower in election years. Altogether, it appears that the political
budget cycle differed before and after the expansion of the franchise in ways that are
consistent with the retrenchment and expenditure switching hypotheses. It is clear, of
course, that many other factors than the differences in the suffrage rules could be behind
this, including the political ideology of the councils' governing parties and macro-
economic trends such as the Great Depression. We consider these and other potential
influences in a later section. First, however, we turn to a systematic analysis of the
data.

<h>EMPIRICAL SPECIFICATION</h>
-----------------------

In an attempt to balance various econometric issues with the data at hand, our model uses
two different estimators. The first is a fixed effect estimator. We cluster the standard
errors at the borough level to take into account the fact that autocorrelation in a fixed
effect model may inflate the z-statistics and cause invalid inference (Bertrand et al.,
2004). The lagged dependent variable may, however, cause a Nickell bias (Nickell, 1981),
since our two samples have only 12 and 16 years of observations, respectively.24 Our
second estimator takes this into account. The GMM estimator (Blundell and Bond, 1998) used
by, e.g., Shi and Svensson (2006), is not ideal in our case as it requires many more cross
sectional units to yield consistent estimates than we obtained. For this reason, we use
the bias-corrected least-squares dummy variable (LSDV) estimator. It performs better than
the GMM estimator in panels with a small cross section (Bruno, 2005a,b).

<h>RESULTS</h>
-------

The main results for the taxpayer suffrage sample are recorded in Table 4 (revenue
outcomes) and Table 5 (expenditure outcomes). The corresponding results for the universal
suffrage sample are reported in Tables 6 and 7. For each fiscal outcome, we report both
the estimates obtained with the fixed effects and the LSDV estimator, which mostly yield
similar results for the election year indicator variable. We find strong evidence of an
opportunistic political budget cycle in both samples but the nature of the cycle is
conditional on the suffrage rules. Under taxpayer suffrage, the political budget cycle
shows up as a reduction in current income and in rate income in the election year (Table
4). Spending on administration is cut in election years. There is no detectable impact on
the relative composition of capital and current spending (Table 5). The cut in
administration is insufficient to balance the books and we find that election years are
associated with lower surpluses (Table 4). In other words, the election year tax cut is
partly funded by cutting back on bureaucracy and partly by running a smaller surplus (or a
small “unplanned” deficit). The magnitude of the tax cut is about £0.6 per 1000 capita
which should be compared to the total income (net of precept) of £15 per 1000 capita. The
reduction in administration corresponds to about a 1.5 per cent cut in the election year.
These are sizable effects which are consistent with the retrenchment hypothesis. We
observe a different pattern under universal suffrage. Most notable are election year
increases in capital expenditure and reductions in current expenditures (Table 7). The
increase in capital expenditure is £0.93 per 1000 capita with the average capital
expenditure being about £5.2 per 1000 capita. The reduction in current expenditure is
somewhat smaller (£0.55 per 1000 capita with average expenditure being £25). This suggests
that the LMBs systematically moved large-scale capital projects to the election year,
while cutting back on current spending. On the revenue side, we find no evidence of a
political budget cycle in tax income or in capital income. There was an election year
drop, however, in current income (Table 6) and a tendency to run smaller surpluses or
larger deficits in election years. Since rate income is unaffected, the fall in current
income can be attributed to election year reductions in user chargers. These findings are
consistent with the expenditure switching hypothesis. The estimations yield some
additional results which are of independent interest. Firstly, the variable wealth is
positively related to current spending and revenues in both samples. This is consistent
with Wagner's Law that relates the size of government to income and wealth (Wagner, 1883).
Secondly, insofar as the variable population captures scale effects, we notice that the
negative point estimate on this variable in the estimations with current (and sometimes
also with capital) expenditure is consistent with decreasing returns to scale in the
production of these services. Millward and Sheard (1995), in their study of the local
finances of 25 provincial municipalities in England and Wales from 1870 to 1914, also find
evidence of (moderate) diminishing returns. Population growth correlates negatively with
revenue and expenditure outcomes, but is only significant in the universal suffrage
sample. In the taxpayer suffrage sample, we control for the size of the electorate with
the variable franchise extension. The boroughs which experienced an extension of the
suffrage (due, for example, to changes in the fraction of property rated for tax purposes)
tended to collect more tax income and to run smaller surpluses (Table 4).

<h>ROBUSTNESS CHECKS</h>
-----------------

In this section, we discuss a number of robustness checks and evaluate some alternative
interpretations of our findings.

<hs>  Partisan cycles</hs>
  ~~~~~~~~~~~~~~~

The opportunistic political budget cycles that we have emphasised above do not make a
distinction between the ideologies of the political parties in power but simply assume
that all parties are primarily interested in getting re-elected. There exists, however, a
well-established literature, beginning with the classical work by Hibbs (1977), Chappell
and Keech (1986), and Alesina (1987), which takes the view that partisan cycles in
economic and fiscal outcomes can emerge because parties have different views on
appropriate policies and their hold on power fluctuates. In the context of budget cycles,
the relevant distinction is between parties on the left which support higher spending and,
with a balanced budget rule, higher taxes; and parties on the right which support lower
spending and taxation. Both before and after the First World War, elections in London were
fought along partisan lines (White, 2001). Before the War, the Progressive Party and the
Moderate Party were the two dominant parties in local elections in London. At the time,
the Progressive Party consisted of a mixture of Liberals, Fabian socialists and radicals
and it generally favoured high (local) government spending. The Moderate Party and, from
1906, The Municipal Reform Party, created by Conservatives and Unionists, were the
dominant right-wing parties. The political landscape changed after the First World War
with the increased prominence of the Labour Party. This undoubtedly had its source in the
Representation of the People Act of 1918 which enfranchised the working-class and gave it
a strong voter base. Consequently, the Labour Party replaced the Progressive Party as the
dominant left-wing party. The right-wing opposition formed a secret anti-Labour pact in
1922 in response to the popularity of the Labour Party in the first election after the
War. To investigate whether partisan cycles were important, we code the dummy variable
left for years in which a notionally left-wing party (the Moderate Party, the Labour Party
or, in one case, the Socialist Party) holds the majority in the borough council and zero
otherwise.25 We conjecture that, if anything, spending and taxation levels should be
higher during the term of a left-wing party. The results are reported in Panel A of Tables
8 and 9 for the taxpayer suffrage and universal suffrage sample, respectively. The
variable left is not significant except for one of the fiscal outcomes: for the taxpayer
suffrage sample, left has a positive effect on current expenditures (at the 10 per cent
level of significance). The evidence for partisan cycles is clearly weak, justifying our
focus on opportunistic cycles. Importantly, controlling for ideology does not affect the
evidence for opportunistic cycles at all: the rise of the Labour Party after the First
World War cannot by itself explain the observed difference in the opportunistic political
budget cycle.

<hs>  Absentee owners</hs>
  ~~~~~~~~~~~~~~~

Under taxpayer suffrage, owners of rated property in a borough were eligible to vote even
if they did not reside in that borough. These absentee voters did not enjoy the benefits
of better local public services to the same extent as resident voters. Accordingly, they
might have been particularly inclined to support retrenchment and economy. It is,
therefore, possible that variations in the fraction of absentee owners could by itself
affect fiscal outcomes under taxpayer suffrage. Unfortunately, we do not have information
on the number of absentee owners/voters, so we use data from the Censuses of 1901, 1911
and 1921 on the number of uninhabited houses as a proxy. The number of uninhabited houses
in the boroughs ranged from 199 to 3283. We have no way of testing how strong the
correlation between empty property and absentee owners is. Nonetheless we see from Panel B
of Table 8 that the variable absentee owners is insignificant for all fiscal outcomes and
that evidence of the opportunistic political budget cycle is as before.

<hs>  The Great Depression</hs>
  ~~~~~~~~~~~~~~~~~~~~

The economic climate in the 1930s was very different to that in the first decade of the
century and in the 1920s. It is possible, therefore, that the Great Depression, and not
the change from taxpayer to universal suffrage, could explain the differences in the
nature of the budget cycle that we observe between the two sample periods. It should be
mentioned here that London and the South East fared comparatively well during the Great
Depression (White, 2001). There were pockets of extremely high unemployment in the capital
but the overall unemployment rate in London was low (Marriott, 1991). As Booth and Glynn
(1975) observed, when national insured unemployment peaked in 1932 at 22.1%, it was 13.5%
in London, 28.5% in the North East, and 36.5% in Wales. Similarly, Hatton (2003) noted
that across the period 1923–1938, average regional rates of unemployment varied from 8% in
London and the South East to around 22% in parts of Wales and Northern Ireland. It is
therefore unsurprising that White has written that the “1920s and 1930s consolidated the
rise in the standard of life of the London working class that the First World War had so
unexpectedly fan-fared” (White, 2001, p. 226). We recall from Figs. 4 and 5 that current
spending and tax income shift upwards around 1930, suggesting that the depression years
triggered a fiscal expansion amongst the LMBs. To investigate if the Great Depression and
the associated jump in spending and taxation contributed to shaping the political budget
cycle during the interwar years, we have re-estimated the model for the universal suffrage
sample with the inclusion of a dummy variable, Great Depression, coded one for depression
years from 1929 to 1937 and zero otherwise. The results are reported in Panel B of Table
9. The dummy variable is positive and significant, as expected, for current spending,
current income and tax income. The depression years were, on average, associated with
larger surpluses. More importantly, the evidence for the political budget cycle from
Tables 6 and 7 is robust after controlling for Great Depression. We conclude from this
that the Great Depression did exert some influence on the public finances of the LMBs but
was not itself responsible for the difference in the nature of the political budget cycle
before and after the extension of the franchise.

<hs>  Heterogeneous election year effects</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The baseline results concern the average election year effect across the 28 LMBs in the
two samples. This may mask important heterogeneity. To investigate this, we have re-
estimated the baseline specification with a set of 28 borough-specific election year dummy
variables. The results are summarized in Tables 10 and 11 which report the coefficient on
the election year dummy for each borough for the two samples. We observe some
heterogeneity as one would expect, but there is no indication that the average results are
driven by one or two outliers. Table 10, with the results from the taxpayer suffrage, is
sorted according to the size of the electorate (franchise extension). While the point
estimates on the vast majority of borough-specific election year effects in the current
income and tax income regressions are negative and significant, there are a few boroughs
where the effect is positive. These are concentrated in boroughs with the most restricted
franchise. This is consistent with the finding in Aidt et al. (2010) that retrenchment is
most pronounced where penny-conscious middle class voters gain control of the councils.

<hs>  Other robustness checks</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

We have checked whether the null result for capital expenditure and capital income in the
taxpayer suffrage sample can be attributed to the large investment recorded for St.
Marylebone in 1905. Excluding this borough from the sample does not affect any of the
results [not reported].

<h>CONCLUSION</h>
----------

The evidence base for the existence of political budget cycles is overwhelming.
Politicians use the fiscal levers granted to them to win re-election if they can. How this
plays out is, unsurprisingly, a function of the institutional constraints imposed on the
elected representatives. As pointed out by Brender and Drazen (2005), Shi and Svensson
(2006) and many others, the political budget cycle is conditional. We contribute to the
literature on the conditional political budget cycle in two main ways. Firstly, the focus
of previous research has been on the period after the Second World War. In contrast, we
enlist data from the early part of the 20th century and find that the political budget
cycle is by no means a recent phenomenon: it was alive and kicking in London both in the
years leading up to the First World War and during the interwar period. Secondly,
precisely because of the emphasis on modern data, previous research explored the political
budget cycle in the context of universal suffrage.26 Our historical perspective allows us
to investigate the nature of the cycle under two different suffrage regimes and we find
that it differs in marked but predictable ways. This strengthens the existing evidence
base that the political budget cycle is contingent on political institutions and rules.
Persson and Tabellini (2003), Streb et al. (2009), and Klomp and de Haan (2012) have
previously demonstrated that election rules, regime types and legislative checks and
balances affect the nature of political budget cycles in modern democracies. Gonzalez
(2002) finds that the political budget cycle in Mexico was magnified as democratic
institutions improve in quality while Potrafke (2012) reports that the cycle is stronger
under two- rather than under multi-party systems. Others have found that the experience of
voters, information flows and fiscal transparency are also important.27 The picture that
emerges from this literature has yet to come into sharp focus, but one lesson is clear:
context is crucial for the incentive and ability of incumbent politicians to manipulate
expenditure and taxes for electoral gain. We have added new evidence to the understanding
of the conditional nature of the political budget cycle by demonstrating that the suffrage
rules themselves matter.


<h>REFERENCES</h>
----------

  [1] Toke S. Aidt, Martin Daunton, Jayasri Dutta. The retrenchment hypothesis and the extension of the franchise in England and Wales. doi:10.1111/j.1468-0297.2009.02344.x
  [4] James E. Alt, David Dreyer Lassen. Transparency, political polarization, and political budget cycles in OECD countries. doi:10.1111/j.1540-5907.2006.00200.x
  [5] James E. Alt, David Dreyer Lassen. Fiscal transparency, political parties, and debt in OECD countries. doi:10.1016/j.euroecorev.2005.04.001
  [7] Marianne Bertrand, Esther Duflo, Sendhil Mullainathan. How much should we trust differences-in-differences estimates?. doi:10.1162/003355304772839588
  [8] Richard Blundell, Stephen Bond. Initial conditions and moment restrictions in dynamic panel data models. doi:10.1016/S0304-4076(98)00009-8
  [9] Alan E. Booth, Sean Glynn. Unemployment in the Interwar Period: A Multiple Problem. doi:10.1177/002200947501000404
  [11] Adi Brender, Allan Drazen. Political budget cycles in new versus established democracies. doi:10.1016/j.jmoneco.2005.04.004
  [12] Giovanni S.F. Bruno. Approximating the bias of the LSDV estimator for dynamic unbalanced panel data models. doi:10.1016/j.econlet.2005.01.005
  [13] Giovanni S.F. Bruno. Estimation and inference in dynamic unbalanced panel-data models with a small number of individuals
  [15] Jakob de Haan, Jeroen Klomp. Conditional political budget cycles: A review of recent evidence. doi:10.1007/s11127-013-0106-6
  [17] James Gillespie. Poplarism and proletarianism: Unemployment and Labour politics in London, 1918-34. doi:10.4324/9781315446684
  [18] Maria de los Angeles Gonzalez. Do changes in democracry affect the political budget cycle? Evidence from Mexico. doi:10.1111/1467-9361.00150
  [20] E. P. Hennock. IV. Finance and politics in urban local government in england, 1835-1900. doi:10.1017/S0018246X00001072
  [22] Douglas A. Hibbs. Political Parties and Macroeconomic Policy. doi:10.1017/S0003055400269712
  [25] Susanne Lohmann. Rationalizing the political business cycle: A workhorse model. doi:10.1111/1468-0343.00035
  [28] ROBERT MILLWARD, SALLY SHEARD. The urban fiscal problem, 1870‐1914: government expenditure and finance in England and Wales. doi:10.1111/j.1468-0289.1995.tb01429.x
  [29] B. R. Mitchell. British historical statistics
  [33] Niklas Potrafke. Political cycles and economic performance in OECD countries: Empirical evidence from 1951-2006. doi:10.1007/s11127-010-9695-5
  [35] Min Shi, Jakob Svensson. Political budget cycles: Do they differ across countries and why?. doi:10.1016/j.jpubeco.2005.09.009
  [36] Jorge M. Streb, Daniel Lema, Gustavo Torrens. Checks and balances on political budget cycles: Cross-country evidence. doi:10.1111/j.1467-6435.2009.00444.x
  [37] Simon Szreter. Economic growth, disruption, deprivation, disease, and death: On the importance of the politics of public health for development. doi:10.2307/2137377
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  [39] Linda Gonçalves Veiga, Francisco José Veiga. Political business cycles at the municipal level. doi:10.1007/s11127-006-9104-2
<ART>A theory of economic development and dynamics of Chinese economy
================================================================

Authors: Saite Lu, Jim H. Shen, Weiping Li, Jun Zhang
DOI: 10.1016/j.econmod.2019.06.003
Year: 2020  |  Pages: 69-87
ASJC codes: 2002
Keywords: Chinese economy, Economic transition process, Heterogeneous outputs, Inefficient SOEs, Private firms, Resource misallocation, Slowing-down, World demand curve

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper constructs a theoretical model which captures the recent slowing-down of Chinese economy. In contrast with the previous literature which largely confines its focus on the resource misallocation between inefficient state-owned enterprises (SOEs) and more efficient private firms under a closed economy setting, this paper re-examines the dynamics of the growth of Chinese economy from the perspective of an open economy. In particular, this paper incorporates heterogeneous outputs and relative prices into the model, where private firms are assumed to be the major exporters and the remaining large SOEs create increasing import demand from the home country. By adding downward sloping world demand curve, our paper predicts a turning point during the transition process, as the falling relative price for exports starts to constrain and eventually slow down the growth; SOEs begin to co-exist with private firms in the economy before it is fully transformed. Our paper provides a theoretical foundation in terms of understanding the current dynamics and institutional change of Chinese economy. Additionally, this paper also provides quantitative evidence on the effects of financial development during the China's economic transition process.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Our paper is related to several studies in the previous literature. The closest work to
our paper is done by Song et al. (2011) who also constructs a growth model to capture the
dynamics of the transition of Chinese economy. The model developed in this paper differs
from the one by Song et al. (2011) in the following aspects: First, instead of assuming
the homogeneous output in the baseline model, our model incorporates heterogeneous outputs
and relative prices into the analysis, with private firms assumed to be the major
exporters and the remaining large SOEs create increasing import demand from the home
country. Second, we add more realistic intratemporal decisions so the domestic
consumption/investment now consists of two different goods. (SOE and Private firm good)
These two extensions allow us to illustrate the relevance of the potential occurrence of a
turning point within Chinese economy, after which the economy would slow down caused by
the co-existence between SOE sectors and private firms. This is drastically contrasted
from Song et al. (2011)'s model in which they predict the remaining SOE sectors would be
crowded out by high-productivity private firms and the whole economic transition process
would be completed smoothly. Lin et al. (1994) argues that the China's economic miracle is
due to the state's appropriate adoption of comparative advantage following development
strategies such that the labour-abundance factor endowment structure of Chinese economy is
fully utilized. Our paper partially agrees with his views; however, it also goes one step
further to ask whether such comparative-following advantage development strategies are
sustainable in the long run. This is because according to the argument in our paper,
comparative advantage following development strategies would inevitably make the exporting
sectors become the priority within the economy and the over-focus on the biased growth
pattern toward exporting would lower the relative price of the home country due to the
more intense competition; this could finally lower the profitability of most of private
firms which are largely concentrated within the exporting sectors. The decline in
profitability of private firms could make the economic growth of Chinese economy in the
long run become unsustainable. Papers by Lardy (2007), Kuijs (2005) and Aziz (2006) have
rationalized various of reasons of why Chinese economy has failed to translated itself
into the consumption-driven economic growth pattern and been heavily cling to the
investment and exporting biased growth mode. For instance, both Kuijs (2005) and Aziz
(2006) illustrate the relevance of the role of income disparity in determining current
growth pattern of Chinese economy. Other scholars include Riedel et al. (2007) and
Boyreau-Debray and Wei (2005) who further argue the underdeveloped financial sector in
China might be one of the fundamental causes of the failure of transformation for Chinese
economy to step toward the consumption-driven economic growth pattern. What sets our paper
apart from their work is that we consider the resource allocation between high-
productivity private firms and low productivity SOEs as the main factor in explaining the
long-run economic performance of Chinese economy and we also incorporate the role of
financial sectors in affecting the growth of Chinese economy into the proposed framework.
Hsieh and Peter (2009) demonstrate slow growth of total factor productivity (TFP) of
Chinese economy since the 2008 is largely caused by the resource misallocation across
private and state sectors, which in turn resulted into the lower aggregate total factor
productivity of Chinese economy. We partially agree with their views in the sense the
damping effect of state-sectors on private counterparts would certainly lead to the
resources flowing into low productivity state sectors, which leads to the resource
misallocation within Chinese economy. Nevertheless, what makes our paper distinctive from
their work is we demonstrate in a growth model to show that resource misallocation would
not only lower the aggregate TFP of Chinese economy, but also directly triggered the
inferior performance of exports as well as the lower productivity of private firms, which
both factors contribute to the slowing-down of Chinese economy. Paper by Hsieh and Song
(2015) further confirm the aforementioned points that, arguing restructuring of large SOEs
and shrinkage of state sectors since the late 1990s to 2008 has been responsible for the
dramatic growth of Chinese economy during the period including 20 percent of aggregate TFP
growth. Paper by Lin et al. (2016) presents a rather optimistic outlook regarding the
future growth prospects of Chinese economy. They argue the current slowing-down of Chinese
economy is more caused by the structural factors external to the Chinese economy, such as
the decline of growth of the rest of the world economy. Although it is true the sluggish
growth of other countries with particular reference to Western economies has been
persistently responsible for the lower growth of Chinese economy, they seem to ignore the
structural factors stemming from the internal issues of Chinese economy such as the
expansion of state-sectors and its ensuing crowding out effect on private sectors. Our
paper argues that the internal and external factors which contribute to the slowing-down
of Chinese economy are inherently intertwined. This is because according to the model
developed in our paper, once the private sectors are crowded out by state sectors, the
external export would be also negatively affected as most of private sectors concentrate
within the exporting sectors. The rest of the paper will be organized as follows: The
second section offers the empirical motivation for our theoretical model. Sections 3 and 4
describe the theoretical model and model simulation results in greater detail.

<hs>  Reverse trend between GDP growth and large SOEs</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Regarding the empirical motivation of this study, the slowing-down of Chinese economic
growth in the recent years is one of the first observations from the data which triggers
the interests of this study. The following Fig. 1 shows the decline in China's annual GDP
growth rate (in constant prices) over the past decade. From Fig. 1, it is apparent China's
annual GDP Growth Rate (in constant prices) has declined from 11.4 percent in 2005 to 6.6
percent in 2018. One of the argument proposed in this paper is that the resource
misallocation caused by the co-existence between private sectors and state sectors is
crucial for us to understand the current slowing-down of Chinese economy. Therefore, it is
important to look at the evolution of the state-sector in Chinese economy. With respect to
the proportions of state sector within the Chinese economy, the data also exhibits some
interesting patterns: Fig. 2 has a adverse trend to Fig. 1. From 2005 to 2007, the number
of SOEs is decreasing while the GDP growth rate increases in this period. From 2011 to
2015, number of SOEs increase and GDP growth rate decreases in this period. This implies
that state sector in China is represented by large SOEs which have co-existed with private
sectors in the past decade, but which might potentially contribute to the resource
misallocation within Chinese economy. One of the most important features of such resource
misallocation is embodied by the huge liabilities against large SOEs. Fig. 3 shows the
increasing tendency of the amount of both liabilities and assets of large SOEs in China
since 2005. Note: Prior to 2007, this number includes all the industrial SOEs. From 2007
to 2011, large SOEs are defined as SOEs whose operating incomes are above 5 million RMB.
After 2011, large SOEs are those whose operating incomes are above 20 million RMB. Note:
All the number has been transferred to the price level of 1999. The dramatic increase in
the amount of liabilities of large SOEs in China since the past decade signifies the fact
the financial sector including banking system is biased towards large SOEs. This gives
large SOEs the priority in of bank loan lending as banks are also stated owned.

<hs>  Impact of co-existence on GDP growth</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In this section, the paper explores the effect of co-existence between SOEs and privately
owned enterprises (POEs) on the GDP growth using empirical analysis. This paper assumes
the co-existence of SOEs impedes POEs’ performance, reduces the export, and decreases GDP
growth.

     <hss>Data and model construction</hss>

        This paper uses the economic data of 31 provinces in mainland China1 between 2005
        and 2017. All the variables in this paper are collected from the regional economic
        database within the Chinese Stock Market and Accounting Research Database (CSMAR).
        The industrial data about private firms begin in 2005 and ends at 2017 in the
        database so that we choose the data from 2005 to 2017. Besides, most of variables
        are converted to the price level of 1999 to reduce the impact of inflation. To
        alleviate the impact of extreme value, all the variables are winsorized at the 1%
        level. To measure the co-existence between SOEs and POEs, this paper employs the
        ratio of operating sales in state-owned industrial firms to that in big-and-
        medium-sized industrial firms. A higher value of co-existence represents SOEs
        occupy a large proportion in the economy. All the variables definitions are
        summarized in Table 1 and the summary statistics are shown in Table 2. According
        to the summary statistics of Table 2, private industrial firms have average 9.6%
        return on total assets and 54.7% leverage in the sample.

     <hss>Crowding out effect of co-existence on POEs’ performance</hss>

        This paper employs ROA of private firms as the first proxy of economic performance
        of POEs and shows the result in Table 3. Model 1 only controls year fixed effect
        and model 2 include the remaining control variables. Coefficients of co-existence
        are negative and significant at the 1% level, indicating a negative effect of co-
        existence on earnings capacity of POEs. In other words, POEs in the provinces with
        high co-existence have lower earnings capacity. The regression result for the
        second proxy for economic performance of POEs is the operating sales of private
        industrial firm is presented in Table 4. Co-existence have negative and
        significant coefficients in model 1 and model 2, proving that co-existence is
        detrimental for the private firms' sales. Combining the results found in Table 3,
        this paper concludes that co-existence has crowding out effect for private firms’
        performance.

     <hss>Impeding effect of co-existence on export</hss>

        In this section, the paper explores the impact of co-existence on exportation
        performance, which is a key driver for economic growth. In Table 5, co-existence
        has negative and significant coefficients with export, illustrating that co-
        existence has a negative relationship with exportation. In other words, a higher
        level of co-existence reduces the total exportation. In the next section, this
        paper examines the impact of co-existence on total exportation and importation.
        Results are presented in Table 6. Coefficients of co-existence are negative and
        significant at 1% level, similar to the results of Table 5. This result
        demonstrates that high co-existence would damage the exportation.

     <hss>Impeding effect of co-existence on GDP</hss>

        In the prior analysis, the empirical results show high levels of co-existence is
        detrimental to the development of POEs and exportation, implying co-existence
        might damage the economic development. To examine this expectation, this paper
        carries out further empirical analysis and presents the result in Table 7 and
        Table 8. Table 7 harnesses GDP as the dependent variable and shows negative and
        significant coefficients of co-existence. This result indicates high co-existence
        impedes the GDP. We employ GDP per capita as the alternative measure for economic
        development and shows the result in Table 8 still has negative and significant
        coefficients, in line with prior analysis. These results prove the detrimental
        effect of co-existence on economic development. Our empirical results find a
        higher level of co-existence impedes POEs’ performance, export performance, and
        economic growth.

<h>THE MODEL</h>
---------

Developing a theoretical framework which is suitable for transition economies like China
would be the key for our analysis. Song et al. (2011) considers a small-open economy model
(SSZ model), which provides a good explanation for the Chinese growth story over the past
20 years. The micro-foundations of their model relies on the OLG model, but they extend
the simple OLG structure with heterogeneous agents (workers and entrepreneurs) and divide
the industrial sector into two types of producers: F firms and E firms. F firms are the
less efficient, financially integrated, and state owned enterprises, while the E firms are
more productive, credit-constrained, private firms. After economic transition takes off,
resources are reallocated from less efficient firms to more efficient ones within the
industrial sector. During the transition periods (i.e. resources are reallocated from F
firms to E firms), the economy keeps accumulating foreign assets, as the aggregate
domestic investment shrinks overtime. The financial development can be reflected by the
falling iceberg costs, or alternatively, an increase in the financial access for E firms.

<hs>  Transition dynamics</hs>
  ~~~~~~~~~~~~~~~~~~~

It also guarantees that E firms prefer delegation to direct control and young
entrepreneurs are motivated to invest their savings in the production of E firms rather
than deposit them in the financial intermediaries. The threshold productivity level is
negatively related to the current relative price. Therefore, when the relative price
falls, the speed of transition gradually slows down and the transition will eventually be
ceased at a certain point. In addition to the capital growth in E firms, employment growth
is also positively related to the growth of price levels. Given the complexity of the
dynamics, quantitative simulation is required to examine the both capital and employment
growth in E firms. This implies that the capital growth rate of F firms relies on the
employment shares of E firms in this economy. If the employment share of E firms grows
faster than the population growth rate (i.e. during the economic transition), the capital
growth in F firms declines, and vice versa.

<hs>  Scenario 1 - adding heterogeneous outputs and relative price</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The calibrated parameters are given in Table 9. Imbs and Mejean (2010) provides cross-
country evidence on the export price elasticity, with the estimates for most of the
country lie between −3 and −4. We choose the upper bound, −3, in the simulation which
provides reasonable dynamics for most of the variables. Furthermore, it seems natural for
us to assume the initial relative price to be 1 in both extensions so they can be
consistent with the baseline model at the initial position. This assumption is also
important for the initialisation of all the other economic variables in all our
simulations. In order to avoid sharp price falls, we take the log form of the total
exports in our price simulation and set an upper limit for the relative price at 1 which
further smooths the price movement during the simulation14. In this simulation, the
growing production from E firms will shift the world supply curve to the right and lower
the relative price after the transition takeoff. This further decreases the rate of return
to capital in E firms and lessens their profitability and entrepreneurial savings.
Therefore, the transition process is slowed down.

<hs>  Results</hs>
  ~~~~~~~

In the baseline model, the transition process is primarily reflected by the growth of the
employment levels in E firms. During economic transition, we expect the efficient E firms
to gradually outgrow the inefficient F firms. This is directly reflected by the baseline
simulation in Panel E and Panel F (Fig. 4). On the contrary, our model experiences
economic growth slow down, the transition slows down after year 1997 in first extension
and, for the second extension, this slowdown comes after year 2000. The slow down in
economic growth and trade activities are indeed observed in China in recent years. Hence
our model better fits the growth experience post 2008 financial crisis. On the other hand,
the employment of F firms are more persistent in our model. E firms face difficulties to
carry on the transition after certain point and F firms keep the dominant position on
employment levels. According to the assumption there is no unemployment in this economy16
and the amount of working-age workers is fixed, the employment shares of E firms and F
firms always add up to the full employment level. This verifies our claims in the
propositions. In our model, the full transition equilibrium is not reached, which means
that life-time earnings of workers are permanently lower than the baseline simulation at
new equilibrium, due to the existence of less efficient F firms. This provides answers to
the puzzling differences between the aggregate consumption/saving of workers in Figs. 6
and 7. The wage differential and entrepreneurial savings are the main drivers to trigger
the economic transition in the SSZ model; now both factors increase by much less in our
model, which inevitably slows down the transition process. Panel E and Panel F in Fig. 5
present staggering differences on the capital account positions among three simulations.
The capital flows in the model are determined by the differences between the domestic
savings and domestic investment. There are drivers behind this: 1. F firms are financially
integrated and its production technology requires higher levels of investment than E
firms. More importantly, the F firms remain dominant; 2. The increasing savings from the
entrepreneurs (managers) are the major sources for the future investment in E firm, as
they are financially constrained, but now the falling relative price discourages the
savings from entrepreneurs by lowering the rate of return in E firms and managerial wage.
Therefore, our model predicts the possibility of capital inflow rather than outflow19
after certain tipping point. This suggests a possibility to rebalance the position of
foreign reserves in a country20. To understand the causes, we need to analyse in more
detail the aggregate saving and investment dynamics in the model. As the aggregate
investment levels are driven by changes of aggregate capital levels, the trend of
aggregate investment in both firms should be consistent with the trend of the aggregate
capital levels in both firms. This is confirmed by Panel D and Panel E (Fig. 6). The
pattern of aggregate investment is dominated by the pattern of the aggregate investment of
F firms in our extensions, while in the baseline, this was dominated by the aggregate
investment of E firms. On the other hand, as we have explained earlier, the savings of
entrepreneurs grow much slower than the baseline model because of the falling rate of
return to capital and managerial wage. This is indeed observed in Panel A (Fig. 6), and
the savings of workers increase by much more in our model. Given the large number of
workers within the economy, the trend of aggregate savings is inevitably dominated by
their savings. The changes in asset levels follow the law of motion. The difference in
aggregate asset positions between our model and the baseline simulation is entirely due to
the lower life-time earnings of workers, as in our model, the transition process reaches
an equilibrium level with the existence of both E firms and inefficient F firms. With less
lifetime earnings, the workers need to accumulate more wealth than the baseline to smooth
their consumption across time. The aggregate asset positions of workers coincide between
two extensions is a direct consequence of the identical long run labour wage. The
differences in the saving levels of workers are due to the different capital stock levels
in E firms and F firms. We noticed that the savings of workers are higher in the
extensions, but they rise less dramatically than the aggregate investment in F firms,
which explains the predictions of net capital inflow in our extensions. The divergence
between the consumption of workers in our extensions and the baseline (Panel B in Fig. 7)
is also caused by the differences of lifetime earnings between the simulation of our
extensions and the baseline simulation. With less earnings, the workers consume less in
our model. The lower consumption levels for entrepreneurs follow a similar logic, as we
have seen in Fig. 5, the managerial wage grows by much less, which results lower
consumption. With lower consumption, the asset accumulation for entrepreneurs appears to
grow faster in our model at the beginning. However, the baseline soon surpasses both
scenarios, as E firms grow much faster and offer increasingly higher managerial wages over
time, which enable the wealth accumulation process to speed up after a certain point.

<h>CONCLUSION</h>
----------

The economic growth in China has been heavily reliant on investment and exports for quite
some time. The failure to translate the benefits of economic growth into domestic
consumption calls for urgent action to rebalance the Chinese economy21. Our model explores
the theoretical possibilities of the Chinese growth experiences with the coexistence of
both SOEs and private firms. Our work also enriches the understanding about the
interactions and interdependence between economic transition and international trade. We
first introduce heterogeneous outputs into the SSZ model by assuming SOEs (F firms) and
private firms (E firms) produce two different products, with the latter specialises in
exporting only. Another major difference is the inclusion of relative price between two
goods and the downward sloping world demand curve. The relative price levels is
endogenised into many key variables, such as the managerial wage, the rate of returns to
capital in E firms, the saving rate of entrepreneurs, and E firm's capital per effective
unit of labour. Therefore, the private firms cannot completely outgrow the SOEs during the
transition due to the falling relative price. If the increasing exports from home country
lowers the relative price to a threshold level the transition process could even come to a
halt. In addition, we develop a more realistic set of micro-level foundations by allowing
intratemporal decisions for the consumption demand of workers and entrepreneurs and the
investment demand of E firms and F firms. The essential idea is to allow domestic
consumers and firms to consume and investment two different goods domestically so that a
falling relative price will also raise its domestic demand. Hence the price movements are
less dramatic than the first extension. Another important result is related to China's
accumulation of foreign reserves and net capital flows. In contrast to the popular
argument that the growing foreign reserves in China are due to the manipulation of its
exchange rates and export-led growth, the financial repression plays a key role in
understanding the foreign reserve accumulation in China. Our model predicts a failure of
full transition. Hence it is compatible with the recent empirical observation. China's
foreign reserves have been falling continuously from US$3.8 trillion in 2014 to US$3.1
trillion in 2017. Net capital outflow at the beginning of economic transition can be
reversed if the transition hits the turning point.


<h>REFERENCES</h>
----------

  [3] Justin Yifu Lin, Guanghua Wan, Peter J. Morgan. Prospects for a re-acceleration of economic growth in the PRC. doi:10.1016/j.jce.2016.08.006
  [5] Zheng Song, Kjetil Storesletten, Fabrizio Zilibotti. Growing like China. doi:10.1257/aer.101.1.196
  [8] Chang Tai Hsieh, Peter J. Klenow. Misallocation and manufacturing TFP in China and India. doi:10.1162/qjec.2009.124.4.1403
  [9] Chang Tai Hsieh, Zheng Michael Song. Grasp the large, let go of the small: The transformation of the state sector in China. doi:10.1353/eca.2016.0005
<ART>Bertrand competition under network externalities
================================================

Authors: Masaki Aoyagi
DOI: 10.1016/j.jet.2018.10.006
Year: 2018  |  Pages: 517-550
ASJC codes: 2002
Keywords: Divide and conquer, Local externalities, Price discrimination, Two-sided markets

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Two firms engage in price competition to attract buyers located on a network. The value of the good of either firm to any buyer depends on the number of neighbors on the network who adopt the same good. When the size of externalities increases linearly with the number of adoptions, we identify the set of pricing strategies that are consistent with an equilibrium in which one of the firms monopolizes the market. The set includes marginal cost (MC) pricing as well as bipartition pricing, which offers discounts to some buyers and charges markups to others. We show that MC pricing fails to be an equilibrium under non-linear externalities in a general network, but identify conditions for an equilibrium with bipartition pricing to be robust against perturbations in the externalities from linearity. The analysis is applied to platform competition in a two-sided market under local and approximately linear externalities.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Goods have network externalities when their value to each user depends on the adoption
decisions of others. Consumption goods such as social networking services, online game and
auction platforms, and social and entertainment events all exhibit positive network
externalities through direct interaction among their users, whereas goods such as computer
OS and housing developments also exhibit positive externalities through the provision of
complementary goods such as applications packages, shops and public transportation.
Externalities are important also for intermediate goods. As argued by Carvalho (2014), for
example, modern production is an intricate network of firms. In such a network, a single
supplier of inputs serves multiple downstream firms who are themselves linked with each
other in the form of mutual production of final products or technology transfers. A
downstream firm would find a higher value for the same inputs as used by other downstream
firms that are linked to it. Despite their importance in reality, our understanding of
network externalities is limited when those goods are supplied competitively. The
objective of this paper is to study price competition in the presence of such
externalities: We formulate a highly stylized model of price competition in which users
located at the nodes of a network experience positive externalities when their neighbors
adopt the same good or technology. In our model, two symmetric firms each supply goods or
technologies that are incompatible with each other. Users of either good experience larger
positive externalities when more of their neighbors in the network adopt the same good. In
stage 1, the two firms post prices simultaneously. The prices can be perfectly
discriminatory and negative, and are publicly observable. In stage 2, the buyers
simultaneously decide which good to adopt or not to adopt either. When no network
externalities are present, it is clear that the unique subgame perfect equilibrium (SPE)
of this game has both firms offer c, the constant marginal cost (MC) of production, to all
buyers. We find that marginal-cost pricing is consistent with an SPE with monopolization
by one of the firms in an arbitrary network when the externalities are linear in the
number of neighbors adopting the same good. In contrast with the case with no
externalities, however, we show that various pricing strategies are consistent with an SPE
under linear externalities. In effect, the necessary and sufficient condition for a price
vector to be consistent with a monopolization SPE is that the sum of markups and markdowns
for any subset of buyers is less than or equal to the externality benefits they
collectively enjoy with the rest of the network. With no markup or markdown to any buyer,
MC pricing satisfies the conditions for an SPE under linear externalities, and so does a
class of bipartition pricing, which entails price discrimination based on a binary
partition of the buyer set: Markups are charged to the buyers in one subset and the
extracted surplus is used to subsidize the buyers in the other subset. The size of a
markup or markdown to each buyer is proportional to the number of his neighbors in the
other subset. When the externalities are non-linear, on the other hand, we show that MC
pricing is consistent with an SPE only when the buyer network is either a cycle or
complete.1 This observation leads us to the study of SPE pricing strategies that are
robust against slight perturbations in the externalities from linearity. Specifically, we
define SPE pricing strategies under linear externalities to be robust if there exists a
non-degenerate set of approximately linear externalities under which there exists an SPE
pricing strategy that is “close” to the original pricing strategy. We show that in a large
class of networks, bipartition pricing given some binary partition of buyers is in fact
robust. One important class of networks that admits a natural interpretation of robust
bipartition pricing identified above is the class of networks that corresponds to two-
sided markets: In these markets, the two firms are platforms that compete in offering
marketplace to agents on two sides, and agents on one side experience externalities only
from the adoption decisions of agents on the other side. We show that there exists an SPE
with cross-subsidization in which all agents on one side are charged markups while all
agents on the other side are offered discounts. Furthermore, the size of the markup or
discount to each agent is approximately proportional to the number of users on the other
side of the market who are directly connected to them.2 As mentioned above, the key
assumption of our model is the ability of the firms to perfectly price discriminate the
buyers. In the application of the current model to a consumption good market, hence, we
interpret each buyer as a collection of consumers in a particular segment of the market
differentiated by geographical locations, gender, past activity records, etc., which is
referred to as a side in Jullien (2011).3 According to this interpretation, pricing is
uniform within each side, but discriminatory across different sides. On the other hand, it
is possible to think of each buyer as a single agent in intermediate goods markets where
the number of participants is typically not so large. One good example is provided by the
international competition in the sales of infrastructures that has recently become a major
form of international trade. In a market for high-speed rails, for example, there are
typically a small number of firms capable of providing a system, a buyer is either a
country or a region and hence is also limited in number, and the good has externalities
since it is not simply a physical product but includes the operation and management of the
system: Countries contemplating the adoption of a high-speed rail would be concerned with
the rail system adopted by their neighbors if future connection between their systems is
anticipated.4 It is well recognized that games with adoption externalities possess
multiple equilibria. In our model, this corresponds to the potential multiplicity of Nash
equilibria (NE) in the subgame played by the buyers after the posting of the prices by the
firms. Our analysis supposes that each firm expects the most pessimistic scenario when
contemplating deviations. Specifically, we consider two extreme NE as follows: The
A-maximal NE is one in which the set of buyers who choose A is maximal in the sense that
buyer i chooses A in it as long as he chooses A in some NE. The B-maximal equilibrium is
one in which the set of buyers who choose B is maximal in the same sense. We suppose that
the buyers coordinate on the B-maximal equilibrium when firm A deviates, and the A-maximal
equilibrium when firm B deviates. Although we avoid the discussion of how such
coordination is achieved, this assumption is shown to support the broadest spectrum of SPE
by minimizing the profitability of deviations, and hence is useful for the identification
of the set of SPE prices. The paper is organized as follows: After discussing the related
literature in Section 2, we formulate a model of price competition in Section 3. Section 4
considers the subgame played by the buyers in stage 2, and Section 5 presents a
preliminary analysis of the two-stage game involving the firms. An example illustrating
the discussion is presented in Section 6. Section 7 provides a characterization of SPE
pricing strategies under linear externalities, whereas Section 8 analyzes the feasibility
of MC pricing under non-linear externalities. The robustness of an SPE under linear
externalities is studied in Section 9. Section 10 concludes with a discussion. All the
proofs are collected in the Appendix.

<h>RELATED LITERATURE</h>
------------------

This paper contributes to two strands of literature. First, it contributes to the
literature on network competition and two-sided markets through the introduction of local
network externalities. Beginning with Katz and Shapiro (1985), most work on the topic
supposes that the externalities are global in the sense that the adoption decision of any
single buyer affects all other buyers equally.5 In the context of two-sided markets, this
implies that the participation of any agent on one side of the market equally affects the
utility of all participating agents on the other side of the market.6 In contrast, we
suppose that the adoption decision of any buyer affects only his neighbors on the network.
In two-sided markets, our formulation implies that the participation of any agent may have
different effects on different agents on the other side of the market.7 Second, it
presents a general analysis of price competition between suppliers of goods with local
network externalities. Models of price competition under local network externalities
include Banerji and Dutta (2009), Bloch and Quérou (2013), Blume et al. (2009), Chen et
al. (2018), Fainmesser and Galeotti (2016b), and Jullien (2011). Blume et al. (2009) and
Bloch and Quérou (2013) study price competition under local network externalities when
market segmentation among the firms is exogenously given. Banerji and Dutta (2009) study
price competition using a graph representation of local externalities when there is no
price discrimination. Chen et al. (2018) formulate a model of differentiated duopoly when
the degree of network externalities is small enough to guarantee a unique NE in the
buyers' game where they choose continuous consumption levels. Fainmesser and Galeotti
(2016b) analyze a model in which two firms with differentiated products compete in price
when they observe the degree of influence some consumers have on other consumers in the
form of network externalities. Most closely related to the present model is Jullien
(2011), which considers a model of Stackelberg price competition between two platforms
under a very general specification of local externalities.8 Although we focus on a more
restricted class of local externalities than in Jullien (2011) in order to derive a more
explicit conclusion, there is a significant overlap in the analysis.9 The multiplicity of
equilibria is often a central concern in games with network externalities.10 Since the
pioneering work of Dybvig and Spatt (1983), this concern has led the literature to focus
on such issues as implementing efficient or revenue maximizing equilibria under complete
and incomplete information, intertemporal patterns of adoption decisions, as well as the
validity of introductory pricing.11 As mentioned in the Introduction, we abstract from the
issue by supposing that whenever there is a deviating firm, the buyers coordinate on its
least favorable NE. The literature makes different assumptions in this regard. For
example, Ambrus and Argenziano (2009) assume that the agents' actions satisfy correlated
rationalizability, which implies that they coordinate on the pareto-efficient alternative,
and Jullien (2011, Assumption 2) assumes that a change in price offer by one firm to
buyers outside its market segment does not affect the decisions of those inside it. One
key idea used in the present paper is that of divide-and-conquer, which has been studied
by Segal (2003), and Bernstein and Winter (2012) among others in contracting problems in
which a single principal offers a contract to the set of agents whose participation
decisions create externalities to other agents.12

<h>ROBUSTNESS OF A BIPARTITION SPE</h>
-------------------------------

The following corollary presents easy-to-verify sufficient conditions for the requirement
in Proposition 9.2, and shows that a robust bipartition SPE exists in a large class of
networks.

<h>DISCUSSION</h>
----------

Our construction of an SPE of the price competition game assumes that a non-deviating firm
becomes focal following any deviation by either firm. While this assumption supports the
broadest spectrum of SPE and serves our purpose, it is not consistent with, for example,
the assumption that the buyers choose the Pareto efficient alternative. However, even if
the buyers coordinate on a less extreme NE, or make adoption decisions sequentially, the
set of SPE prices will be a subset of the set of SPE prices identified in the present
analysis. The essential feature of the market for goods with network externalities is the
multiplicity of equilibria. In the present context, this corresponds to the multiplicity
of NE in the buyers' subgame. Fundamental multiplicity of equilibria also exists in the
pricing game between the firms when the externalities are linear. In this case, any
pricing strategy is consistent with an SPE as long as the sum of markups and markdowns for
any subset of buyers does not exceed the externality benefits they collectively enjoy with
the rest of the network. We show that MC pricing is not consistent with a monopolization
SPE unless the network is a cycle or complete under generic externalities. Unfortunately,
however, positive identification of SPE pricing strategies is difficult under generic
externalities: Equilibrium pricing subtly depends on the network configurations and
externality specifications, and it appears difficult to obtain a general principle. We
show that bipartition pricing is consistent with an SPE under linear network
externalities, and identify conditions under which it is robust to slight perturbations in
externalities from linearity. There are a number of interesting extensions of the present
model. A firm contemplating competing in the sale of network goods should naturally be
concerned about uncertainty associated with the large multiplicity of equilibria as
discussed above, and may take action to alleviate the problem before entering such a
market. For example, a firm may try to design its product so that it will have stronger
externalities than the competing products, or a positive degree of compatibility with
them.49 It would also be interesting to consider alternatives to the assumptions of
perfect price discrimination, public observability of prices, and perfect knowledge of the
firms about the network.50 For example, while standard, the assumption that all the prices
are perfectly observed by all buyers is strong, and it is interesting to examine what
happens when the firms can choose to post its price to each buyer privately.


<h>REFERENCES</h>
----------

  [1] Attila Ambrus, Rossella Argenziano. Asymmetric networks in two-sided markets. doi:10.1257/mic.1.1.17
  [2] A. Banerji, Bhaskar Dutta. Local network externalities and market segmentation. doi:10.1016/j.ijindorg.2009.02.001
  [3] Shai Bernstein, Eyal Winter. Contracting with heterogeneous externalities. doi:10.1257/mic.4.2.50
  [4] Francis Bloch, Nicolas Quérou. Pricing in social networks. doi:10.1016/j.geb.2013.03.006
  [5] Lawrence E. Blume, David Easley, Jon Kleinberg, Éva Tardos. Trading networks with price-setting agents. doi:10.1016/j.geb.2008.12.002
  [6] Ying Ju Chen, Yves Zenou, Junjie Zhou. Competitive pricing strategies in social networks. doi:10.1111/1756-2171.12249
  [8] Philip H. Dybvig, Chester S. Spatt. Adoption externalities as public goods. doi:10.1016/0047-2727(83)90012-9
  [10] Bruno Jullien. Competition in multi-sided markets: Divide and conquer. doi:10.1257/mic.3.4.186
  [11] Michael L. Katz, Carl Shapiro. Network externalities, competition, and compatibility
  [12] Donald M. Topkis. Supermodularity and complementarity
  [13] Ilya Segal. Coordination and discrimination in contracting with externalities: Divide and conquer?. doi:10.1016/S0022-0531(03)00114-5
  [14] Xavier Vives. Nash equilibrium with strategic complementarities. doi:10.1016/0304-4068(90)90005-T
<ART>Biomarkers as precursors of disability
======================================

Authors: Apostolos Davillas, Stephen Pudney
DOI: 10.1016/j.ehb.2019.100814
Year: 2020
ASJC codes: 2001
Keywords: Biomarkers, Disability, Prediction, Self-assessed health, Understanding Society

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Some social surveys now collect physical measurements and markers derived from biological samples, in addition to self-reported health assessments. This information is expensive to collect; its value in medical epidemiology has been clearly established, but its potential contribution to social science research is less certain. We focused on disability, which results from biological processes but is defined in terms of its implications for social functioning and wellbeing. Using data from waves 2 and 3 of the UK Understanding Society panel survey as our baseline, we estimated predictive models for disability 2–4 years ahead, using a wide range of biomarkers in addition to self-assessed health (SAH) and other socio-economic covariates. We found a quantitatively and statistically significant predictive role for a large set of nurse-collected and blood-based biomarkers, over and above the strong predictive power of self-assessed health. We also applied a latent variable model accounting for the longitudinal nature of observed disability outcomes and measurement error in in SAH and biomarkers. Although SAH performed well as a summary measure, it has shortcomings as a leading indicator of disability, since we found it to be biased in the sense of over- or under-sensitivity to certain biological pathways.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

An important recent development in research based on large-scale social surveys is the
integration of physical health measurements and markers derived from biological samples,
in addition to traditional self-reported health assessments. Biomarkers are objectively
measured and evaluated as indicators of normal biological or pathogenic processes (Colburn
et al., 2001), and they have potential advantages over self-assessments as early
indicators of conditions that are below clinical diagnostic thresholds, or are pre-
symptomatic and below individuals’ threshold of perception (Colburn et al., 2001).
Cardiovascular, metabolic, inflammatory, neuroendocrine and other biomarkers have been
shown to be predictors of mortality and morbidity when used alone or alongside self-
reported health assessments (Idler and Benyamini, 1997; Gruenewald et al., 2006; Ridker,
2007; Jylhä, 2009; Doiron et al., 2015). They have also been used to reveal the
socioeconomic gradient in health risks (Seeman et al., 2004; Lee et al., 2015; Carrieri
and Jones, 2017). Despite their advantages, biomarkers impose significant additional costs
of collection in the survey context and their potential contribution to economic and
social research is not entirely clear. The wider social impacts of ill-health – on quality
of life, personal and social functioning, and social costs of disease – depend critically
on the duration and severity of disability prior to death, and there has been little
research on the role of biomarkers in relation to disability. Disability is associated
with loss of employment, early retirement and serious consequences for the families
affected (Pudney et al., 2011; Jones, 2016; Christensen and Gupta, 2017) and typically
implies long-lasting impairments that may prevent independent living and generate large
social costs. This is particularly so in the UK where disability prevalence is well above
the European Union average (Jones, 2016) and has been rising rapidly (from 11.9 to 13.3
million over 2013/14–2015/16 (DWP, 2017). There is evidence of an increasing birth-cohort
trend in functional difficulties for older individuals of low socio-economic status
(Morciano et al., 2015) and developed countries like the UK may face severe problems in
supporting the projected future growth in the disabled population and providing public
support to people with care needs (Commission on Funding of Care and Support, 2011). A
crucial question for researchers and policymakers is whether the demand for care services
will be curbed by gains in disability-free life expectancy alongside the projected
continuing gains in longevity. An answer to this question requires a better understanding
of the processes leading to disability, allowing the development of strategies and
screening programmes to address disability more efficiently. The availability of biomarker
information in population-representative data may contribute to that better understanding.
Despite the importance of disability trends for social policy planning, relatively little
is known about the association between biomarkers and future disability. The World Health
Organization (WHO) proposed a framework that portrays progression from diseases to
functional disabilities (WHO, 1980), and Fried et al. (1991) hypothesized the existence of
pre-clinical disability as an intermediate stage in which health impairments have an
impact on general functioning. Few studies have explored the predictive role of biomarkers
in relation to this disability process, and most are limited by being based on small
samples or unrepresentative data (Brex et al., 2002; Reuben et al., 1999; Baylis et al.,
2013; Seeman et al., 1994; Kallaur et al., 2017); or focused exclusively on older
individuals (Reuben et al., 1999; Seeman et al., 1994; Baylis et al., 2013); or concerned
with disability outcomes from a specific disease or condition (Brex et al., 2002; Kallaur
et al., 2017). Another study by Pagan et al. (2016) tests the hypothesis that disability
is a potential mediator in the link between obesity and job satisfaction. We examined the
predictive power of a wide range of biomarkers for future disability and specifically
asked whether biomarkers offer incremental value in predicting disability outcomes beyond
the contribution of the conventional self-assessed health (SAH) measure. SAH may be
associated with disability outcomes in parallel with biomarkers by reflecting the impact
on the individual of diagnosis of health conditions defined in terms of elevated
biomarkers (Idler et al., 2004; Jylhä, 2009), or through bodily sensations that are
sensitive to the biochemical processes measured by biomarkers (a, 2009). Besides
confirming the value of biomarkers as leading indicators of disability, we also
investigated the success of SAH as an overall summary of biomedical states relevant to
disability and examined whether SAH is biased in the sense of over- or under-sensitivity
to specific biological pathways. The paper makes several new contributions to the research
literature. To the best of our knowledge, this is the first study that provides a
comprehensive analysis of this kind. Using baseline data from early waves of the UK
Household Longitudinal Study (UKHLS, also known as Understanding Society), we estimate
predictive models for disability two to four years ahead, exploiting a large set of nurse-
collected and blood-based biomarkers. These biomarkers measure adiposity, grip strength,
blood pressure, lung, kidney and liver functions, inflammation, steroid hormone levels,
blood sugar and anaemia, giving an unusually broad picture of individuals’ health states.
The use of several alternative disability measures demonstrates the robustness of our
results. In addition to simple prediction models, we also develop a latent variable (LV)
approach which is new to the literature. This LV model has a number of advantages. First,
unlike simpler prediction models, it takes into account the longitudinal nature of our
data on disability, allowing for correlation between disability variables two to four
years after baseline. Second, it addresses measurement error bias by allowing for
measurement noise in both SAH (Crossley and Kennedy, 2002) and the biomarkers (Zang et
al., 2015). Measurement error in biomarkers normally causes attenuation of the estimated
impact of the biological pathways on disability, and the LV model is expected to give more
accurate estimates of these impacts. This may be of particular importance for developing
policy strategies and interventions to reduce the personal and social burden of
disability. Third, our LV approach is set up to identify any distinct dimension of health
which influences future disability and is captured by the biomarkers but missed by SAH.
The pattern of factor loadings tells us what underlying aspects of health tend to be
under- or over-represented by the SAH measure and can therefore guide the interpretation
of research findings related to SAH.

<h>DATA</h>
----

The UKHLS is a large, nationally representative panel survey, running continuously from
the initial wave in 2009–10, with each panel member interviewed annually. Its predecessor,
the British Household Panel Survey (BHPS) was incorporated into the UKHLS from wave 2. A
set of physical health measures and non-fasted blood samples were collected by nurses,
five months on average after the wave 2 interview for UKHLS respondents and similarly at
wave 3 for the BHPS sample (McFall et al., 2014). Respondents were eligible for nurse
visits if, at the relevant wave, they were aged 16 or over, lived in England, Wales or
Scotland and were not pregnant. Blood sample collections were further restricted to those
who had no clotting or bleeding disorders and no history of fits. Participants gave
informed written consent for their blood to be taken and stored for future scientific
analysis. The UKHLS has been approved by the University of Essex Ethics Committee and the
nurse data collection by the National Research Ethics Service (10/H0604/2). We define wave
2 as the baseline for the main UKHLS panel and wave 3 as the baseline for the BHPS sub-
panel and we refer to the timing of this baseline observation as t = 0; these baseline
observations were spread through calendar years 2010–2013. We used baseline data on
personal and household characteristics and bio-medical measures as predictors of
disability observed subsequently at waves 4–6 for the UKHLS sample (t = 2, … 4) or waves
5–6 for the BHPS sample (t = 2, 3), where t denotes years since the baseline main
interview. We did not use data from t = 1 since the time gap between collection of
biomarkers and interview at t = 1 was less than 6 months for 75% of the t = 1 sample.
There were 15,632 and 5053 UKHLS and BHPS respondents who participated in the wave 2 or
wave 3 nurse visits. For the UKHLS group, 13,404, 12,719 and 11,434 were followed up at
waves 4, 5 and 6 respectively and had non-missing information on disability; 4513 and 4113
of the BHPS subsample were followed up at waves 5 and 6. We further conditioned the
analysis on the absence of reported disability at baseline by excluding those reporting
the relevant type of disability at baseline. Exclusion of these cases reduced the
potential samples by 25%, 13% and 8% depending on the disability concept used. A detailed
summary of available sample sizes is given in the Supplement Table S1.

<hs>  Biomarkers</hs>
  ~~~~~~~~~~

Measures of adiposity, grip strength, heart rate, blood pressure and lung function were
collected during visits by trained nurses. We used the waist-to-height ratio (WHR) to
measure adiposity. Grip strength was measured (in kg) using a hand dynamometer (McFall et
al., 2014) and we took the highest reading from three repeated measurements for the
dominant hand. Higher levels of grip strength are indicative of better physical
functioning. Three repeated measurements of resting heart rate (HR), systolic and
diastolic blood pressure (SBP, DBP) were taken at intervals of one minute (McFall et al.,
2014). We skipped the first reading, believed to impose upward biases, and computed HR,
SBP and DBP as the average of the second and third readings. HR, which is sometimes
regarded as a measure of fitness rather than health, was used as a continuous variable,
and we also used a binary hypertension indicator recording SBP > 140, DBP > 90 and/or
current use of anti-hypertensive medications (Johnston et al., 2009). Lung function,
assessed using spirometry equipment, was measured by the total amount of air forcibly
blown out after a full inspiration (forced vital capacity; FVC), higher values indicating
better lung function (Gray et al., 2013). Forced expiratory volume in one second (FEV1) is
often used as an alternative to FVC. However, different equipment and measurement
protocols were used in Scotland than in England and Wales, and comparison of matched
samples showed FEV1 to be seriously affected by this, while FVC measures appeared
comparable. Consequently we retained the Scottish sample and used FVC as our lung function
measure. We used blood-based biomarkers specific to inflammation, steroid hormone,
cholesterol, blood sugar, kidney function, liver function and anaemia. C-reactive protein
(CRP) rises as part of the immune response to infection and is associated with general
chronic or systemic inflammation. We excluded those with a CRP over 10 mg/L, because those
values may reflect current transient infections rather than chronic processes (Pearson et
al., 2003). Dihydroepiandrosterone suphate (DHEAS) is the most common steroid hormone in
the body, considered as one of the primary mechanisms through which psychosocial stressors
may affect individual health. Low levels of DHEAS are associated with cardiovascular (CVD)
risks and all-cause mortality (Ohlsson et al., 2010). High-density lipoprotein cholesterol
(HDL) is known as “good” cholesterol, low levels being associated with increased CVD risks
(Wannamethee et al., 2000). Glycated haemoglobin (HbA1c) measures blood sugar, and is
regarded as a validated diagnostic test for diabetes (WHO, 2011). The estimated glomerular
filtration rate (EGFR), calculated from the serum creatinine concentration, measures
kidney function; higher EGFR levels indicate better kidney function (Levey et al., 2009).
We used albumin, the main protein made by the liver, as a liver function test; low albumin
levels suggest impaired liver function (Howard and Sparks, 2016). Haemoglobin (Hgb), is an
iron-containing protein responsible for carrying oxygen throughout the body, and was used
to proxy anaemia status; lower levels of Hgb are suggestive of anaemia (Balarajan et al.,
2012). In addition to specific markers, we also used two composite summary measures. One
was an index of multi-system risk that measures the wear and tear on the body,
approximating the allostatic load (Seeman et al., 2008). Our index combined the selected
biomarkers for inflammation, blood pressure, HR, HbA1c, HDL cholesterol, albumin, DHEAS
and the WHR (Seeman et al., 2008; Howard and Sparks, 2016). HDL, Albumin and DHEAS were
converted to negative values to reflect ill health, and then each biomarker was
transformed into z-scores and summed to calculate the overall index. The second index was
a cumulative risk score for CVD, created by adding the relevant z-scores for WHR, blood
pressure, HbA1c and CRP (Walsemann et al., 2016). A summary of all biomarkers by reported
future disability state is given in the Supplement Tables S3 and S4.

<hs>  Self-assessed health</hs>
  ~~~~~~~~~~~~~~~~~~~~

SAH is considered a summary measure capturing the way that numerous aspects of health,
both subjective and objective, are combined within the perceptual framework of the
individual respondent (a, 2009). The SAH question asked respondents to rate their health
on a five-point scale from “excellent” to “poor”. It was collected in the self-completion
instrument at baseline, approximately five months prior to biomarker collection. We group
the lowest two SAH categories because of their small sample size, giving a four-point
scale ranging from 1 = “excellent” to 4 = “fair” or “poor”.

<hs>  Disability measures</hs>
  ~~~~~~~~~~~~~~~~~~~

Our measures of disability were collected at UKHLS waves 4–6, so disability outcomes were
observed for prediction horizons of t = 2 …4 years for the main UKHLS sample or t = 2, 3
years for BHPS respondents. Respondents were asked about any long-standing physical or
mental impairment that they might have and then the consequent functional difficulties,
from a list of twelve provided (see Supplement Table S2 for the full list). We used the
report of any functional difficulty as a dichotomous variable and the number of functional
difficulties (coded as an ordinal variable: 0, 1, 2 or 3+) as an indicator of severity.
Specific difficulty with mobility is also examined as a separate dichotomous indicator
because of its relatively high prevalence and significance for functioning and
independence in later life (Guralnik et al., 1993). Our fourth disability measure came
from the income module of the UKHLS questionnaire, constructed as a binary indicator of
whether the respondent received income from private disability insurance or any of the UK
disability benefit programmes. For all programmes, receipt requires a decision to apply
for the benefit, the ability to craft a good-quality application and a positive assessment
of need by the programme administrators. Consequently, while the benefit receipt indicator
involves a rigorous external assessment of severity, that assessment is confounded to some
degree by the incentive and capacity to apply for the benefit, which has a strong
socioeconomic gradient (Hancock et al., 2016).

<hs>  Covariates</hs>
  ~~~~~~~~~~

The explanatory covariates that we used in our models have been found to be associated
with disability (Hernández-Quevedo et al., 2008; Morciano et al., 2015), and also directly
with biomarkers (Carrieri and Jones, 2017). The covariates were collected at baseline and
are described and summarised in the Supplement Table S5. Gender and polynomials in age
were used to capture demographic influences. Three indicators of socio-economic status
were included: educational attainment, home ownership and household income. We excluded
disability benefits from income to avoid spurious correlation arising from the fact that
disability creates eligibility for those benefits (see Morciano et al. (2015)). We also
controlled for marital status, household composition, national and urban dummies. To
assess the impact on future disability of lung function over and above smoking status, we
estimated models with and without the inclusion of smoking variables.

<h>METHODS</h>
-------

Our analysis uses a sample of individuals who had no observed history of disability at
baseline defined as the time of biomarker collection (t = 0). Conditioning the analysis in
this way focuses attention on the transition from full physical functioning to disability,
and it avoids the complications raised by the fact that, for people already disabled at
baseline, we do not observe the evolution of their health and disability prior to joining
the Understanding Society panel. In addition to the three binary indicators, we also
extended model (1) to analyse the reported number of functional difficulties as a 4-level
ordered probit model. Average marginal impacts of SAH and biomarkers on the probabilities
of reporting 2+ or 3+ difficulties were then constructed from the estimated ordered
probit. We did not use all 12 specific biomarkers simultaneously as predictors in model
(1), for three reasons. First, there was a significant loss of usable data when all
markers are required to be observed. Second, the full set of health measures (SAH and
biomarkers) displayed a substantial degree of collinearity, so there would have been a
further loss of statistical precision. A third policy-relevant reason for considering each
biomarker separately is that, in practice, it is unlikely that any screening programme
would simultaneously check blood pressure, adiposity, blood sugar, cholesterol,
haemoglobin, hormone levels, liver, kidney and lung function; so there is a practical
interest in the predictive power of each specific marker on its own. However, we also
separately used the two composite indexes for allostatic load and CVD risk to consider the
potential performance of more comprehensive tests. Although models like (1) are fairly
standard in the literature, they are vulnerable to measurement error bias. Biomarkers and
SAH are best seen as noisy indicators of the relevant health concepts rather than direct
observations of those concepts. SAH may be subject to transient random variations in mood
and perception, while biomarkers are affected by random variations in blood samples and
measurement processes. Measurement noise may bias estimates of predictive models like (1),
usually causing attenuation of the estimated impact of biomarkers and SAH. Our alternative
latent variable approach offers a way of dealing with measurement error, by exploiting the
multiplicity of biomarkers that reflect to varying degrees the underlying health state.
Our aim here is to develop a form of the LV model that gives a clear indication of the
predictive value of the biomarker information beyond that contained in the SAH measure. We
used a two-factor structural LV model in which a latent variable hi0 reflects a dimension
of general health at baseline, measured to varying degrees by SAH and the set of twelve
biomarkers (not the indexes for allostatic load and CVD risk). To capture the incremental
contribution of the biomarkers, we specified a second latent health variable, bi0
representing any dimension of baseline health that the biomarkers succeed in measuring,
but which is not captured by SAH. The outcome variables, Di2, Di3, Di4, represent
disability 2, 3 and 4 years after baseline; the correlation between them is captured by an
unobserved random effect, ui, which may have different impacts in different periods. The
resulting model has the structure shown in Fig. 1 and set out algebraically in the
Supplement.

<hs>  Simple predictive models</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~

The results for model (1) at horizon t = 4 are presented in Table 1, which shows the
percentage impact on the predicted number of people classified as disabled, of a
1-standard deviation increase in the relevant biomarker. Columns three (one or more
functional difficulties), six (mobility) and seven (benefits) of the table were derived
from binary probit models; each cell in those columns was based on a separate model for
the relevant combination of biomarker and disability measure. The cells in each row of
columns four and five came from the same ordered probit model for the number of reported
disabilities, with the impact of each biomarker evaluated respectively at the 2+ and 3+
thresholds. First note that, when SAH was excluded from the prediction models, almost all
biomarkers had substantial and statistically significant (at least at the 5% level)
predictive power. The exceptions were for hypertension, DHEAS, EGFR and Hgb, where
estimates were insignificant at the 5% level for some disability measures. When dummy
variables for SAH status were introduced into the model, the magnitudes of the biomarker
coefficients fell, mostly by 20–40%, but generally remained statistically significant.
Consequently, the SAH measure succeeded in capturing some of the predictive power of the
more objective measures, but far from all. There was some variation across biomarkers but,
overall, the nurse-collected and blood-based biomarkers were comparable in terms of their
predictive power. As expected, biomarkers for which higher values represent worse health
states had a positive percentage impact on future disability and vice versa. Note that
lung function, which emerged as a strong influence on disability, was not acting as a
proxy for smoking, since inclusion of smoking variables left the estimated effect
practically unchanged. This is of particular interest given recent evidence of the strong
predictive value of smoking on future disability (Bengtsson and Nilsson, 2018). To save
space, the results for shorter prediction horizons (t = 2, 3) are reported in the
Supplement (Tables S6–S8); they show systematic predictive power for most of the
biomarkers, with the effects mostly rising for longer prediction horizons. To test whether
the predictive role of each biomarker and/or SAH vary by demographic and socioeconomic
status (household income, education and house tenure), we tested the relevant interaction
terms across our different model specifications. The tests found no systematic differences
in the predictive role of biomarkers and SAH on future disability by age, gender or
socioeconomic status. For example, P-values for the interactions of allostatic load with
gender range between 0.471 and 0.716 across the 4-year prediction models of the different
disability outcomes; for interactions with age, P-values ranged between 0.211 and 0.898.
We also found no systematic interactions of our socioeconomic status variables with
allostatic load (P-values between 0.170 and 0.905). Both composite biomarker measures gave
strong effects, with allostatic load having the strongest impact. The results for the
benefit receipt measure of disability were an interesting exception to this: when SAH was
included in the model, the magnitude of the biomarker effect halved and retained
significance only at the 10% level. There may be two behavioural factors involved in that
result. One is justification bias – receipt of benefit may lead some respondents to report
a worse state of health in SAH to justify their receipt of disability benefit.
Alternatively, some people may be reluctant to accept or admit that their health is poor,
leading them both to under-represent their current health difficulties in SAH and avoid
claiming their potential entitlement to disability benefit. Both of these behaviours would
be likely to strengthen the empirical SAH effect relative to the estimated effect of
allostatic load or CVD risk indexes (which are more highly correlated with SAH than
individual biomarkers, and therefore more affected by bias in SAH). Figs. 2 and 3 compare
the magnitude of the SAH and biomarker impacts calculated from models where both SAH and
the relevant biomarker were use as predictors (together with the covariates X). The SAH
impact was calculated as the mean predicted impact of switching the individual from the
best (“excellent”) to worst (“poor/very poor”) category of SAH; with the exception of the
binary hypertension marker, the biomarker effect was calculated as the mean impact of
switching from a value approximately 1.5 standard deviations better to 1.5 standard
deviations worse than the mean (between the 5th and 95th percentiles). Impacts are
calculated using the covariates X for each sampled individual and then averaged. Figs. 2
and 3 (see also Table S9 of the Supplement) show that the biomarkers with statistically
significant impacts shown in Table 1 made predictive contributions of about 20–25% of the
SAH effect in most cases. For disability measures based on the number of disabilities
reported and mobility difficulties, allostatic load made the largest contribution to
prediction, both absolutely and as a proportion of the SAH impact: the impact of a three
standard deviation change in allostatic load was approximately one third that of the
hypothetical SAH shift. For the mobility-based disability criterion, allostatic load and
WHR had the largest impacts in absolute terms (roughly 40% of the SAH effect). In
accordance with the results in Table 1, allostatic load contributed less to the prediction
of benefit receipt, while the markers for grip strength, adiposity and lung function all
gave substantially greater impacts (around one third of the SAH effect). Despite some
differences between disability definitions in the pattern of results, the overall
conclusion seems robust – biomarkers made a contribution to prediction of disability four
years ahead that is significant both statistically and in terms of absolute magnitude. But
that contribution is moderate in comparison with the information contained in SAH. There
is a risk that the act of observation could change the behaviour being observed – that
formal or informal feedback about the respondents’ biomarker levels may prompt additional
GP consultations and treatments for previously undiagnosed health conditions, or
behavioural changes (Zhao et al., 2013). In the UKHLS, survey nurses were instructed not
to discuss or interpret respondents’ results in general or in relation to other people in
the survey, and blood tests results were not available to survey participants. However,
participants received a Measurement Record Card with their blood pressures, height,
weight, waist circumference, percent body fat, and grip strength. The survey protocol
(National Centre for Social Research, 2010; McFall et al., 2014) also specified tailored
blood pressure feedback: respondents were informed and advised to visit a GP within 2
months, 2 weeks or 5 days if their blood pressure was mildly raised (140≤ systolic blood
pressure <160 or 90≤ diastolic blood pressure <100), moderately raised (160–180 or
100–115) or considerably raised (over 180 or over 115), respectively. Those with normal
blood pressure measurements received reassuring feedback. To explore the robustness of our
results to the possibility of feedback effects, we carried out a number of sensitivity
analyses. First, we added the categorial blood pressure feedback variable to all our
predictive models, and found that the results remained practically identical to those
presented in Table 1 and Figs. 2 and 3. We also interacted the categorical blood pressure
feedback variable with our biomarkers, finding the interaction terms statistically
insignificant (at the 10% level) across all models. For example, the P-values of
interaction terms between our composite biomarker measure (allostatic load) and the
categorical blood pressure feedback variable range from 0.678 and 0.904 across the
different disability outcome models. Thus the predictive role of biomarkers does not
systemically differ between those who were informed of an elevated blood pressure and
those with normal blood pressure levels. We also re-estimated the prediction models after
excluding respondents who received feedback of mildly, moderately or considerably raised
blood pressure, showing only minor differences to our base case results (compare Tables S9
and S10 of the Supplement). Overall, this evidence alleviates concerns about potential
distortions from survey feedback effects – although it is disappointing from the policy
perspective that there is so little evidence of feedback generating health improvements.
This bleak result is consistent with recent evidence suggesting that screening programmes
providing health information are often relatively ineffective as a means of disease
control (Chang et al., 2018; Kim et al., 2019).

<hs>  Do SAH and biomarkers measure the same thing? Latent variable results</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our finding that SAH is a strong predictor of future disability parallels similar evidence
on mortality risks (Glei et al., 2014; Idler and Benyamini, 1997; Jylhä, 2009), but it
raises the issue of how SAH relates to more objective biological aspects of health. SAH is
a subjective response that may reflect bodily sensations produced by biological disease
processes, but also potentially many other things such as mood, self-image, past contacts
with the healthcare system, and health shocks to friends and relatives (Idler and
Benyamini, 1997; Jylhä, 2009). If used for policy purposes, SAH might also be reported
subconsciously or strategically to achieve or justify a particular outcome. Even in its
relation to biological processes, SAH may be biased in particular directions since not all
disease processes are equally apparent to the sufferer. No single biomarker or composite
biomarker index can plausibly act as a direct comparator in a conventional measurement
error validation study (Bound et al., 2001). A more productive approach is to use
biomarker information alongside SAH to indicate the biological pathways to which SAH is
insufficiently or excessively sensitive.1 We use the LV approach outlined in Section 3 to
integrate SAH and biomarkers within an appropriately broad measurement setting. In
practice biomarkers are also potentially error-prone measures, although not vulnerable to
the behavioural reporting biases that may affect SAH. Random measurement errors in
biomarkers used as predictors cause bias for the purposes of estimating causal links
between health and future disability. But that bias is not a problem if we are concerned
with prediction in the context of policy applications such as screening or monitoring
programmes, since the biomarkers available to programme administrators are subject to the
same measurement error process – the (causally biased) prediction model still gives the
best prediction of future disability conditional on biomarker information as observed by
the administrator. However, to understand the relationship between SAH and biological
disease pathways we need estimates more closely related to the true causal processes. An
advantage of the LV model is that allows for measurement noise in both SAH and biomarkers
and so avoids measurement error bias stemming from classical random measurement error.
Tables 2 and 3 summarise results from the LV model. Table 2 gives the estimated factor
loadings relating observable biomarkers to the two latent dimensions of health. Except for
the binary hypertension measure, the loadings were normalised to give the impacts of
latent health on observed indicators in standard deviation units. The loadings of the
primary latent health factor hi0 are mostly as expected, with disability risk raised
significantly by WHR, hypertension, CRP and HbA1c; and lowered by grip strength, lung
capacity, HDL cholesterol, DHEAS, EGFR and Albumin. The loadings on the second latent
factor b must be interpreted carefully in relation to the SAH loadings. For any given
marker, if the loading on h has the correct sign and the loading on b has the same sign,
then this implies that the health concept implicitly captured by SAH understates the role
of the biological pathway which the marker measures. Under this interpretation, our
finding is that SAH strongly understates the importance of grip strength, lung function,
DHEAS and liver function and weakly understates the effect of CRP. If the loading on h has
the correct sign and the loading on b has the opposite sign, then SAH can be interpreted
as over-emphasising the pathway measured by the marker. This was the case for WHR,
hypertension and HDL cholesterol and, more weakly, for HbA1c and EGFR. In two cases, HR
and Hgb, the loading on h was small, with an a priori wrong sign, which was strongly
reversed in the loading for b. This finding can be interpreted to mean that, in these
dimensions, SAH is a potentially misleading indicator of future disability. Our finding
from the simple predictive model (1) was that biomarkers provide significant and
substantial predictive power which is nevertheless moderate in relation to SAH. The same
result is also evident in results from the LV model. Table 3 gives summary statistics for
the predictive probabilities of future disability conditional only on SAH and covariates
(π1(X, S)), and conditional on SAH, covariates and twelve biomarkers (π2(X, S, B1 … B12)).
These predictive probabilities were calculated for all disability definitions and
prediction horizons. For three of the predictors, the mean predicted probability of
disability rose as we varied the prediction horizon from t = 2 to t = 4, by approximately
20% (1 or more functional difficulties), 28% (mobility problem) or 62% (benefit receipt).
This rise in disability risk over time is a natural reflection of the cumulative character
of disability prevalence. However, there was no such rise in prevalence measured as the
proportion of individuals reporting two or more functional difficulties. For all four
disability measures, the predictive probabilities also became substantially more variable
(their standard deviations increased) as the prediction horizon lengthened. For (almost)
all of the predictions, there was a rise in the variability of the predictor when we
expanded the baseline predictor set by adding the biomarkers. This reflects the fact that
adding biomarkers gives a more detailed and diverse picture of each individual's
disability risk. The correlations between π1 and π2 were generally high, reflecting the
good – but not perfect – performance of SAH as a general health proxy.

<h>DISCUSSION AND CONCLUSIONS</h>
--------------------------

We investigated the predictive power of objective nurse-collected biomeasures and blood-
based biomarkers for functional disability, following individuals who reported no
disability at baseline for up to four years after collection of the health measures. We
used a wide range of biomarkers, and alternative measures of disability, covering the
existence and number of functional disabilities, mobility difficulties and receipt of
disability benefits. For almost all of the biomarkers, we found 4-year-ahead predictive
effects that were substantial in magnitude and statistically significant. When SAH was
introduced as a predictor alongside the biomarkers, the magnitude of the biomarker effects
fell, in most cases by 20–40%, but remained important in magnitude and highly
statistically significant for most of the biomarkers examined. Although there were some
differences across biomarkers and disability measures, we found that measures of
adiposity, grip strength, heart rate, lung functioning, cholesterol levels, inflammation,
blood sugar and anaemia had strong predictive power for future disability risk, over and
above SAH. How should we interpret these predictive results? Causality and predictability
are not the same thing, and there is a possibility that the association between health
measures and future disability outcomes is partly the result of unobserved factors. In our
view, causality can never be established unambiguously in observational data but, compared
to cross-section analysis, the 4-year gap between our initial health measure and
disability outcomes makes it much more likely that the predictive effects are causal
rather than proxy in nature. This separation in time removes the possibility of reverse
causation and weakens any ability of baseline biomarker levels to proxy omitted
heterogeneity. Moreover, the most likely non-causal channels of association appear not to
be important here – we found no evidence of an effect of health information fed back to
respondents, nor of smoking behaviour on disability outcomes. It is also important not to
over-emphasise the importance of causality. Predictability is extremely important for some
major policy purposes – for example, a successful screening programme needs a good
predictor to identify priority population groups, and that does not necessarily require a
complete structural understanding of all the biochemical, behavioural and environmental
processes involved in determining the target outcomes. In addition to simple predictive
models, we also developed a new latent variable approach capable of incorporating large
numbers of biomarkers and longitudinal observation of disability outcomes, while allowing
for measurement error in SAH and biomarkers. This approach allowed us to identify
distortions in SAH as a measure of health, by detecting an additional predictive factor
that is revealed by the biomarkers but not by SAH. The corresponding factor loadings
indicate dimensions of biological function that are given too much or too little weight by
SAH in predicting disability. We found that SAH is excessively sensitive to the biological
pathways reflected in adiposity, hypertension and cholesterol, and insufficiently
sensitive to strength, lung function, hormonal balance and liver function. Nevertheless,
SAH emerged as a good general health proxy in the sense that, when SAH and biomarkers were
both used as predictors, the estimated biomarker impacts on future disability, although
substantial absolutely, were moderate in comparison with the effects of SAH. For example,
using a composite summary measure to proxy allostatic load (our strongest biomarker
predictor), we found that moving from the best (excellent) to worst (fair/poor) category
of SAH increased the risk of disability 4 years later by 5–18 percentage points on
average, depending on the disability concept used, while an increase in allostatic load
from the fifth to the lowest 95th percentile (roughly a 3-standard deviation rise)
increased disability risk by 2–7 points.

<hs>  Limitations</hs>
  ~~~~~~~~~~~

Key strengths of our analysis come from its use of UKHLS data which allowed us to use a
large, nationally representative sample covering all adult ages. The bio-social character
of UKHLS provided a wide range of nurse-collected and blood-based biomarkers, in addition
to SAH, disability indicators and extensive measures of household characteristics and
socio-economic status. This adds breadth and depth to the small body of evidence that
already exists on biomarkers as predictors of future disability. Existing studies are more
limited in terms of the range of biomarkers used and also the study population, which is
mainly restricted to older people, nonrepresentative samples or specific patient groups
(Brex et al., 2002; Reuben et al., 1999; Baylis et al., 2013; Seeman et al., 1994). As far
as we are aware, ours is the first study that makes an explicit evaluation of subjective
SAH against objective biomarker information in relation to disability. Despite these
advantages, there are limitations. First, the available data follow individuals for a
relatively short time horizon. We have found evidence of a rise in the estimated effect of
biomarkers as the length of the prediction horizon increases, suggesting that our results
may understate the full long-term predictive role of biomarkers. Second, functional
disability is a slippery, hard-to-measure concept and the measures used in our analysis
are necessarily limited. Our use of a range of alternative disability measures alleviates
these concerns to some degree, but a complete solution requires further research. Finally,
although we used an unusually extensive set of biomarkers, the multidimensional nature of
the biomedical processes underlying disability means that there may remain significant
aspects of physical health that are not covered by our analysis.


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<ART>Boundedly rational consumers, energy and investment literacy, and the display of information on household appliances
================================================================================

Authors: Julia Blasch, Massimo Filippini, Nilkanth Kumar
DOI: 10.1016/j.reseneeco.2017.06.001
Year: 2019  |  Pages: 39-58
ASJC codes: 2002
Keywords: Bounded rationality, Energy label, Energy literacy, Energy-efficiency, Energy-using durables, Online randomized controlled trial

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

It is an ongoing debate how to increase the adoption of energy-efficient light bulbs and household appliances in the presence of the so-called ‘energy efficiency gap’. One measure to support consumers’ decision-making towards the purchase of more efficient appliances is the display of energy-related information in the form of energy-efficiency labels on electric consumer products. Another measure is to educate consumers in order to increase their level of energy and investment literacy. Thus, two questions arise when it comes to the display of energy-related information on appliances: (1) What kind of information should be displayed to enable consumers to make rational and efficient choices? (2) What abilities and prior knowledge do consumers need to possess to be able to process this information? In this paper, using a series of (recursive) bivariate probit models and three samples of 583, 877 and 1375 households from three major Swiss urban areas, we show how displaying information on the future energy consumption of electrical appliances in monetary terms (CHF), rather than in physical units (kWh), increases the probability that an individual makes a calculation and identifies the appliance with the lowest lifetime cost. In addition, our econometric results suggest that individuals with a higher level of energy and, in particular, investment literacy are more likely to perform an optimization rather than relying on a decision-making heuristic. These individuals are also more likely to identify the most (cost-)efficient appliance.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The residential sector consumes nearly 30% of the total final energy consumption in
Switzerland and about 58% of the energy end-use consumption of households is based on
fossil fuels (BFE, 2015). Improving the energy efficiency in the residential sector is
therefore one of the strategies to reduce total fossil energy consumption and related
CO2-emissions in Switzerland. While a major effort needs to be made to reduce the
consumption of heating fuels, there is also a potential for enhanced energy efficiency in
the electricity consumption of Swiss households. One important pillar of reducing
residential electricity consumption is to foster the adoption of energy-efficient lighting
and household appliances. A low adoption of energy-efficient technologies is often related
to the ‘energy-efficiency gap’ (Sanstad and Howarth, 1994a; Howarth and Sanstad, 1995;
Allcott and Greenstone, 2012), i.e. the frequent observation that individual decision-
makers do not choose the most energy-efficient appliance, even if this appliance is also
the most cost-efficient choice from the individual's point of view (minimizing lifetime
operating costs).1 The list of potential underlying causes for the ‘energy-efficiency gap’
is long and includes a myriad of market and behavioral failures (Sanstad and Howarth,
1994b; Broberg and Kazukauskas, 2015). A large body of literature studies, for example,
(implicit) subjective discount rates and their role for the persistence of the energy
efficiency gap (Hausman, 1979; Train, 1985; Coller and Williams, 1999; Harrison et al.,
2002; Epper et al., 2011; Bruderer Enzler et al., 2014; Min et al., 2014). In this paper,
we abstract from subjective discounting and other market and behavioral failures to focus
on those market and behavioral failures that are related to the provision and processing
of energy-related information. In order to choose between two similar electrical
appliances, a rational, utility-maximizing consumer should solve an optimization problem
in order to choose the appliance that minimizes the sum of the purchase price and the
present value of future energy costs (Sanstad and Howarth, 1994a,b; Gerarden et al.,
2015). This optimization requires knowledge on the purchase prices of the appliances to
choose from, the electricity consumption of the respective products, the expected
intensity and/or frequency of use, the expected lifetime of the appliance as well as
current and future electricity prices. If markets provide too little or inadequate
information about these parameters, or if this information is not salient enough to the
consumer, this constitutes a barrier to solving the optimization problem (Sanstad and
Howarth, 1994a). In fact, in many purchase situations, the information about the energy-
efficiency of an appliance and thus about the future energy costs is less salient than the
purchase price. However, even if information on the energy consumption of the appliance is
provided, the optimization regarding the lifetime cost of an appliance depends on
additional information as mentioned above. To carry out the optimization, the consumer
needs to gather the required information and then process this information correctly. This
creates both ‘information cost’ and ‘optimization cost’ (Conlisk, 1988), given that the
consumer needs to deliberate upon the options to choose from. Acknowledging the presence
of ‘deliberation cost’ (Pingle, 2015) is equivalent to acknowledging that individuals are
‘boundedly rational’ (Simon, 1959; Sanstad and Howarth, 1994a), which means that they are
not always able to acquire and process all the necessary information to trade-off all the
alternatives in real decision-making situations. This is because information acquisition
is costly and the processing of information is cognitively burdensome. As a consequence of
being boundedly rational individuals tend to have problems solving the optimization
problem when making an investment decision. Instead, they often rely on simple rules of
thumb or decision heuristics (Wilson and Dowlatabadi, 2007; Frederiks et al., 2015), which
potentially widens the energy efficiency gap.2 Against the background of the described
information-related market and behavioral failures, the research presented in this paper
deals with the question how information on future energy consumption should be displayed
on products in order to enable consumers to identify the appliance that minimizes lifetime
cost. Furthermore, we investigate whether and to what extent cognitive abilities as well
as energy and financial literacy support consumers in identifying a cost-efficient
appliance. We hereby assume that consumers may follow two different types of decision-
making strategies: One is to optimize over the lifetime cost of the appliance. This is in
line with the neoclassical concept of a fully rational and informed consumer. The other
type of decision-making strategy, which is in line with the concept of bounded
rationality, is heuristic decision-making, i.e. choosing an appliance according to a
specific and salient characteristic of the appliance, e.g., a low purchase price, a high
energy-efficiency rating or a lower physical energy consumption. The choice of the
decision-making strategy is determined, on the one hand, by the information that is
readily available in the purchase situation, e.g., in the form of information display on
the products. On the other hand, it is determined by an individual's ability to process
the available information, which is influenced by socioeconomic factors as well as the
individual's level of energy and investment literacy. The latter determine the individual-
specific deliberation cost. We thus assume, that the deliberation cost are a function of
energy and investment literacy, with energy literacy being defined as the individual's
prior energy-related knowledge, such as knowledge about energy prices and energy
consumption of different appliances, and investment literacy being defined as the
individual's cognitive ability to perform an investment analysis. To examine the role of
information display, energy and investment literacy on the choice of electrical appliances
of boundedly rational consumers, we organized a household survey and conducted two online
randomized controlled trials with simple decision tasks. In two experiments, respondents
were presented two similar appliances and had to determine which of the two minimizes
lifetime cost. With these experiments we thus did not elicit consumers preferences but
their ability to calculate the lifetime cost of the appliances.3 Individuals were randomly
assigned to a treatment in which yearly energy consumption of the appliances was displayed
in either monetary terms or physical units. In the empirical part of the paper, we analyze
the individual decisions in the experiments while accounting for the respondents’ energy
and investment literacy, their attitudes towards energy conservation, as well as their
sociodemographics. Drawing on three samples of 583, 877 and 1375 households from three
major Swiss urban areas the data is analyzed in a series of (recursive) bivariate probit
models. We find that displaying information on energy consumption in monetary terms rather
than in physical units positively influences the probability to perform an investment
analysis which in turn increases the probability to choose the most (cost-)efficient
appliance. Also a higher level of energy and investment literacy clearly enhances the
individuals’ probability to do an investment calculation and to choose the most efficient
appliance. This supports the view that both displaying monetary information on future
energy consumption as well as consumers’ prior knowledge and cognitive abilities are
decisive factors when attempting to reduce the energy-efficiency gap. Investing in
consumer education to increase their energy and investment literacy could thus be an
important element in a set of policy measures to enhance residential energy efficiency.
The remainder of the paper is organized as follows. Section 2 presents a literature review
and discusses the theoretical considerations and hypotheses. The dataset and the
experimental design is presented in Section 3 and the econometric specifications are
presented in Section 4. Section 5 presents the results and Section 6 concludes.

<hs>  Information, rationality and the choice of efficient appliances</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Are individuals able to make fully rational decisions by minimizing total lifetime cost
when choosing electric appliances? Or are they ‘boundedly rational’ (Simon, 1959) and
therefore lack the cognitive abilities to perform the optimization task? The discussion
about rational decision-making in the domain of energy efficiency and the role of
information in the choice of efficient appliances is going on for a while (Sanstad and
Howarth, 1994a,b). McNeill and Wilkie (1979) and Anderson and Claxton (1982) investigate
how the provision of information about energy consumption in either monetary or physical
units impacts on the choice of household appliances. While both studies do not find
significant effects of information display, more recent studies do so. For example,
Heinzle (2012) examines the impact that different ways of disclosing energy-related
information have on the choice of TVs in online experiments in Germany. The effects of
three different disclosure formats of energy labels on appliance choice are compared:
annual energy consumption in terms of physical units (kWh), annual energy operating cost
in monetary terms and lifetime energy operating cost in monetary terms. Heinzle (2012)
shows that individuals tend to overestimate potential cost savings between two TV sets if
provided with information on energy consumption in physical units. When disclosing energy
consumption in monetary terms, respondents’ willingness to pay (WTP) for energy efficient
TV sets only increased when lifetime energy cost but not when annual operating cost were
displayed. The display of annual operating cost in monetary terms even reduced WTP
compared to the display in physical units. Similar results are reported in Deutsch (2010):
based on a randomized field experiment on a commercially operating price comparison
website it is shown that disclosing the life-cycle cost of an appliance instead of the
purchase price induces consumers to purchase cooling appliances that are on average 2.5%
more efficient than in the absence of life-cycle cost disclosure. Also Newell and
Siikamäki (2014) test the effects of different forms of energy efficiency labeling. Among
other features, they evaluate the impact of a label including the estimated yearly
operating cost versus the impact of a label including physical information on energy use.
Based on a choice experiment among 1214 US home owners, they find that providing
information on estimated yearly operating cost is more effective in enhancing willingness
to pay for more efficient water heaters than providing information about energy use in
physical units. These findings are partly in line with the findings in Heinzle (2012),
except that in the study of Newell and Siikamäki (2014) the display of annual operating
cost (as opposed to lifetime operating cost) had a positive influence on the choice of
more efficient appliances. For light bulbs, Min et al. (2014) test the influence of energy
labeling on implicit discount rates in an incentivized choice experiment among 168 US
residents and also conclude that the provision of information on annual operating costs of
the bulbs increases consumers’ WTP for more efficient bulbs. Allcott and Taubinsky (2015)
tested the effect of simultaneous information about yearly and lifetime energy cost on
consumers’ choices of either compact fluorescent (CFL) or incandescent light bulbs. In
both an online and an in-store experiment, they provide information about yearly and
lifetime costs of the bulbs to a treatment group. While the treatment increases the market
share of CFLs by about 12% in the online experiment, a similar treatment in the in-store
experiment seemed less effective. Although the effects of displaying yearly and lifetime
energy cost cannot be separated in their experiments, their results further support the
view that providing monetary information supports consumers in accounting for operating
cost. Other studies consider the role of energy-efficiency rating scales on the choice of
appliances. The results of these studies suggest that the information on energy use
provided on energy labels tends to be disregarded in the presence of a rating scale. Both
the results presented in Waechter et al. (2015) and Hille et al. (2015) indicate that the
display of an energy-efficiency rating scale on electric appliances may divert attention
from the information on actual energy consumption of the products, suggesting that the EU
energy label in its current form is used as a decision-making heuristic by many consumers,
rather than supporting a rational and informed decision making.4 Houde (2014) reaches a
similar conclusion. He finds evidence that an energy label can act as a substitute for
more precise information on energy consumption of an appliance and that consumers that
rely on the energy label often overestimate the energy savings associated with the
certified product.

<hs>  The role of energy literacy and education for appliance choice</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Another potentially important prerequisite for rational decision-making in the domain of
electric appliances is energy literacy, which can be defined as an individual's ability to
make informed and deliberate choices in the domain of household energy consumption. In the
literature, energy literacy is defined as a comprehensive concept that has a cognitive, an
affective and a behavioral dimension (DeWaters and Powers, 2011). According to DeWaters
and Powers (2011), energy literacy thus comprises of (1) knowledge about energy production
and consumption as well as its impact on the environment and society, (2) attitudes and
values towards energy conservation as well as (3) corresponding behavior. In this paper,
we use a narrower definition of energy literacy that mainly reflects the individual's
knowledge about energy prices and the energy consumption of different household
appliances. This is because our main goal is to examine what knowledge and cognitive
abilities consumers need to have in order to identify cost-efficient appliances. With
respect to investments in energy-efficient appliances, an additional component gets
relevant: investment literacy, i.e. the individuals’ ability to perform an investment
analysis and hence to correctly evaluate different investment alternatives, for example
when choosing appliances or when deciding about energy-saving renovations. Regarding this
ability, the literature on financial literacy is informative. Lusardi and Mitchell (2009)
show, for example, that more educated people are more likely to correctly answer a
question on compound interest and that this indicator of financial literacy has a relevant
influence on economic decisions in several domains: inter alia, individuals who know about
interest compounding are 15 percentage points more likely to be retirement planners
(Lusardi and Mitchell, 2007). In a study on financial literacy in Switzerland, Brown and
Graf (2013) find that respondents scoring high on financial literacy are more likely to
have an investment related custody account and to make voluntary retirement savings. One
of the first studies that investigates the effect of energy and investment literacy on
electricity consumption in a large sample is the study of Brounen et al. (2013). They
examine the effect of energy and investment literacy on household conservation behavior
and energy consumption in an online survey in the Netherlands. Their indicators for energy
and investment literacy are three items capturing the households’ awareness of the amount
of their monthly gas/electricity bill, the respondents’ choice in a decision between two
alternative heating systems with different levels of energy efficiency, and the answer to
the question whether the household uses green electricity. They find that older and male
respondents are more likely to know about their gas bill and that more educated
respondents are more likely to make a rational investment decision in the heating system
example. However, Brounen et al. (2013) do not find that energy literacy has an impact on
energy conservation behavior among the sampled households in terms of thermostat settings,
and also not on the overall electricity and gas consumption of the household. In addition,
there seems to be a role for education more generally when it comes to energy-related
decision-making. Some studies find a positive correlation between an individual's level of
education and energy literacy or energy-related investment literacy. For example, Mills
and Schleich (2010) find that education, among other socio-economic characteristics, is
positively correlated with knowledge about energy efficiency labels on appliances. In
another study, Mills and Schleich (2012) build an energy-related knowledge index and find
that the knowledge index increases when the most educated member of the household has an
university degree, whereas a high-school degree does not have any effect and vocational
training has a negative effect on the knowledge index. Also Nair et al. (2010) report from
a Swedish sample that a higher level of education as well as a better knowledge about
energy efficiency measures in buildings increases the likelihood that a household invests
in building envelope measures. Apart from the study of Brounen et al. (2013), there is
only little research about the role of energy literacy and energy-related investment
literacy on investment decisions in the domain of residential electricity consumption. In
particular, we are not aware of any study that investigates the impact of energy and
investment literacy on the choice of household appliances. This paper therefore
contributes to the existing literature along three dimensions: first, further empirical
evidence is provided on the role of displaying monetary information about the energy
consumption of an appliance for the choice of electrical appliances. Second, according to
our best knowledge, this is one of the first studies which analyzes the impact of the
level of energy literacy on the choice of electrical appliances and the impact of energy
literacy, investment literacy and monetary information on the choice of the decision
making strategy (optimization vs. heuristic decision making). Lastly, we also analyze the
impact of the decision making strategy on the choice of the appliance in a recursive
model.

<hs>  Theoretical considerations and hypotheses</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In the following, we provide some theoretical reasoning that can explain the role of
energy information display, energy literacy and financial literacy on the choice of
appliances. According to household production theory (Deaton and Muellbauer, 1980)
households purchase inputs such as energy and capital (i.e. household appliances) and
combine them to produce outputs which are the desired energy services such as cooked food,
washed clothes or hot water. These energy services appear as arguments in the household's
utility function (Muth, 1966; Flaig, 1990). The utility function of a household is based
on the consumption of both energy services and all other goods and is maximized under the
budget constraint. A high level of expenditure for energy services will reduce the options
to consume all other goods. Therefore, when facing the choice of light bulbs or household
appliances, consumers are confronted with the optimization problem of choosing the
appliance that provides the desired energy service at the minimum lifetime cost. Consumers
wish to reduce their overall expenditure for energy services and to maximize their
opportunities to consume all other goods, otherwise they experience a loss in utility.5
For the minimization of lifetime cost consumers have to consider the purchase price and
future operating costs of the appliance, which depend on the energy consumption of the
appliance (in Watts), the lifetime of the appliance, the frequency and intensity of use of
the appliance as well as on current and future electricity prices.6 Lifetime cost and
intensity of use cannot be predicted with certainty in the moment an appliance is
purchased, so the individual needs to form expectations regarding lifetime cost and
intensity of use for each appliance within the set of appliances to choose from. The
process of forming expectations and comparing the expected lifetime cost of several
appliances requires time and other resources that can be considered as ‘decision cost’
(Pingle, 2015). To study the role of ‘decision cost’ for the choice of the decision-making
strategy and for the choice of an appliance, we provide a simple 2-period-model of
expectation formation that explicitly takes decision costs into account. This model is
based on the model in Conlisk (1988) and assumes that an individual assesses the expected
lifetime cost of an appliance before purchase.7 Similar as in Conlisk (1988), we assume
that the individual faces two potential sources of a loss that he or she wants to
minimize: (i) experiencing a loss in inter-temporal utility by either underestimating the
lifetime cost of an appliance in period 1 and thus not allocating enough of the budget in
period 2 on the consumption of the energy service, or, by overestimating the lifetime cost
of an appliance in period 1 and thereby restricting consumption of other goods in period 1
itself due to the individual's budget constraint, and (ii) spending too much time and
resources on decision making itself. The lifetime cost of the appliance that was estimated
after having invested the optimal amount of units T★ for decision making can thus be
expressed as L(T★) and can be considered as a realization of the random expectation
variable E(L(T)). Next, we assume that we can define R as the rational expectation of L
and that individual j's estimate E(L(T)) of R is a weighted combination of two elements: a
free estimator f, that is based on a simple rule of thumb and is thus generated without
any decision cost, and a costly improvement of f denoted as r(T), that depends on the time
spent on deliberation. We further assume that the individual makes his or her decision as
if the costly improvement r(T) was as accurate as a sample mean of T independent
observations taken from a distribution with mean R and variance σ2 and as if f was as
accurate as a sample mean of S independent observations which represents a lower number of
draws taken from the same distribution with mean R and variance σ2. The intuition here is
that for an individual who performs a detailed analysis, it would imply drawing a large
number of T thoughts from the distribution with mean R and variance σ2 thereby increasing
the probability that he or she arrives close to R which is the rational expectation of L.
However, in a heuristic approach (rule of thumb), the judgment can be considered to be
based upon only a small number of S thoughts, which can a priori be assumed to be
objectively biased (note that from the point of view of the individual, the guess itself
may be considered unbiased; otherwise he or she would make a different guess altogether).
It is obvious that the lower bound for the optimal time spent on deliberation T★ is at
least 0. This equation gives us some insight into the optimality of different decision-
making strategies. Consider the case when an individual has a lower capacity to perform a
calculation task (i.e. higher β) and the analysis is costly relative to the size of the
problem (large C/σ2) to the extent that the initial guess is reliable (large S). If these
conditions hold with enough force, the corner solution T★ = 0 applies and the individual
spends no resources on deliberation but only follows the rule of thumb f which in this
case is good enough. By definition, α has an upper bound of 1 when the corner solution T★
= 0 applies, i.e. when individual's rule of thumb choice is good enough. Eq. (6) can be
seen to cover both the extremes; when T★ goes to infinity, the expected lifetime cost
converges to the rational expectation R. On the other hand, when T★ = 0, i.e. when α = 1,
the expected lifetime cost is the free estimator f. Depending upon the different
parameters, an individual could be lying anywhere between the range of unboundedly
rationality and a rule of thumb approximation (Conlisk, 1988). The estimation of the
lifetime cost of the appliance will thus be more closer to the rational expectation R as α
gets smaller. From Eq. (7), α is the lower the lower β, i.e. the lower the individual's
effort needed to perform the estimation of lifetime cost of the appliance the lower C
relative to σ2, i.e. the lower the decision making cost related to the complexity of the
problem the lower S, i.e. the lower the amount of (costless) best guesses spent on
estimating R, i.e. the less reliable the rule of thumb Any individual having to decide
between several appliances on offer will first assess the lifetime cost of all the
appliances separately and then, in a second step, compare them to identify the one with
the minimum lifetime cost. From the above-described model, we derive two hypotheses with
respect to whether the individual deliberates or follows a rule of thumb when comparing
the appliances (choice of decision-making strategy). As a natural consequence, but not
directly related to the above theoretical model, we can identify two more hypotheses in
relation to what determines whether the individual successfully identifies the most cost-
efficient appliance (choice of cost-efficient appliance). First, we expect that
individuals with a higher level of energy and investment literacy are more likely to
choose an investment analysis as the decision-making strategy as the process of
deliberation is less costly to them, i.e. a lower β in the theoretical model (H1a). We
further assume that disclosing yearly energy consumption in monetary terms (CHF) rather
than in physical units (kWh) decreases the value of C and hence increases the probability
that the individual carries out an investment analysis rather than following a heuristic
decision-making strategy as this lowers the per unit cost of deliberation (H1b). In a
second step when an individual compares the lifetime costs of two appliances, we expect
that an individual that carries out an investment analysis is more likely to identify the
more cost-efficient appliance (H2a). In addition, we expect that disclosing yearly energy
consumption in monetary terms increases the probability that the individual identifies the
more cost-efficient appliance, again, as the display of monetary information lowers the
per unit cost of deliberation (H2b). Our hypotheses can be summarized as follows: H1a: The
level of energy and investment literacy has a positive impact on the individuals’ ability
to follow an optimization strategy rather than a heuristic strategy. H1b: Displaying
information on the yearly energy consumption of an appliance in monetary terms rather than
in physical units has a positive impact on the individuals’ ability to follow an
optimization strategy rather than a heuristic strategy. H2a: Opting for optimization as
the decision-making strategy has a positive impact on the probability to identify the most
cost-efficient appliance. H2b: Displaying information on the yearly energy consumption of
an appliance in monetary terms rather than in physical units has a positive impact on the
probability to identify the most cost-efficient appliance.

<h>EXPERIMENTAL DESIGN</h>
-------------------

We use an explanatory research approach in order to examine the role of information,
energy literacy, and investment literacy on the choice of the decision-making strategy for
choosing an electrical appliance as well as on the ability to identify the appliance with
the lowest lifetime cost. For this purpose, we have organized a web-based survey in which
two online randomized controlled trials were embedded. The survey was organized in
cooperation with three Swiss electricity providers operating in three major urban areas in
Switzerland (Lucerne, Bellinzona, Biel/Bienne). The two online experiments were part of
the online survey, which was conducted among electricity and gas customers during the year
2015. For this survey, customers of the electricity providers were invited with a letter
accompanying one of their electricity (or gas) bills to access an online questionnaire.8
The invitation letter was sent to a total of 50, 000 (Lucerne), 30, 000 (Bellinzona) and
38, 000 (Biel/Bienne) customers of which 1999 (Lucerne), 958 (Bellinzona) and 1308 (Biel)
accessed the survey page (corresponding to response rates of 4% (Lucerne), 3.2%
(Bellinzona) and 3.4% (Biel/Bienne)). After accounting for the correct target group,9
incomplete responses, and duplicate entries, we have valid and complete data for 1375
(Lucerne), 583 (Bellinzona) and 877 (Biel) survey respondents.10 The three observed
samples should relate to the Swiss population living in urban (and sub-urban) areas. Among
people who accessed the survey page, dropouts primarily happened either because they did
not provide their customer number with the electrical utility (which they had to fill in
at the beginning of the survey), or if they were disqualified as not being part of the
target group of the survey. Of all respondents who started the online survey, filled in
their customer number and were filtered-in as the target group, almost 85% completed the
survey and we do not find any significant selection among the sample of usable surveys
relative to the target group. Next we compare the available basic demographic
characteristics of the three urban areas with the sample population relating to households
reached via the survey (Table 1). In terms of gender and age-groups, the population
represented by the surveyed households seems comparable to the overall population in the
three cities, except in Bellinzona where the share of young population is higher and that
of the elderly is lower. The average number of people living in a household seems to be
higher in our sample, especially in Bellinzona. Other deviations include the Biel/Bienne
sample having a larger living space per person. Bellinzona seems to have more people per
room on average whereas Biel/Bienne has less people per room on average than represented
by the respective population statistics. Finally, we find that two-person households as
compared to one-person households are slightly over-represented across all three samples
(data not shown in the table). It is to be noted that the statistics at the city level may
not completely reflect the statistics of the surveyed areas, i.e. the service areas of the
utilities, which usually also include neighboring municipalities. As the availability of
information about socioeconomic variables at the city level is limited, we also compare
other crucial attributes with the information available at the national level. The share
of respondents who donated money to an environmental organization within the 12 months
preceding the survey is largely in line with the share reported for the Swiss population
(42%).11 The average Swiss household income in 2013 was CHF 10′052. The household income
across our samples is recorded as income categories and about 50% of the households fall
in the category representing an household income between CHF 6′000 and CHF 12′000.
Considering this discussion and the low response rates, we acknowledge that our sample may
not be completely representative of the population living in these regions on all socio-
economic dimensions. However, note that a selection issue in this context could be
considered less of a concern since we are working in a multivariate framework and are
focused primarily on the treatment effects. Nevertheless, generalizations of the results
to the entire Swiss population should be considered carefully. One of the two experiments
was embedded towards the end of the online surveys. Customers of the utilities in
Bellinzona and Lucerne saw Experiment 1, customers of the utility in Biel/Bienne saw
Experiment 2. Survey respondents who saw Experiment 1 were asked to imagine a situation in
which they had to replace a light bulb in their living room. As a replacement, they were
shown two bulbs that differed in their purchase price, power, lifetime, electricity cost
as well as energy efficiency rating (A versus C rating). The information display
corresponded to the current version of the EU energy label for light bulbs (see Fig. 1).
It is important to note that the two described bulbs only differed in price and energy-
related characteristics but not in their color temperature and brightness.12 Respondents
were randomly assigned to two different treatments. In Treatment 1, the information on
energy consumption of the two bulbs was displayed in terms of physical consumption (kWh)
per 1000 h, as it is displayed in the current version of the EU energy label. In Treatment
2, energy consumption was again displayed in monetary terms, i.e. in the form of an
estimate of the energy cost per 1000 hours (in CHF, see Fig. 1). Additionally, we
controlled for order effects by randomly changing the order of presentation of the two
light bulbs in both treatments. Respondents were asked which of the two light bulbs would
minimize their expenditure for lighting during 8 years of planned usage. Thus, as already
discussed in the Introduction, our online experiment is not a hypothetical stated choice
experiment but an online randomized controlled trial with the goal of real calculations of
lifetime costs of the appliances from an objective point of view under different
conditions. In principle, the result of the comparison of lifetime cost will also be
driven by the individual's subjective discount rate. Assuming that the average participant
of our study is not familiar with the concept of discounting and would need a calculator
to incorporate discounting in the analysis, we refrained from providing respondents with a
‘reference discount rate’ that they should use. Instead we assumed that consumers, in case
they opted for an investment analysis, would consider the undiscounted future operating
cost to evaluate the lifetime cost of the two bulbs. Also Allcott and Taubinsky (2015)
present undiscounted operating cost in an online experiment on consumers’ choices of light
bulbs, presumably for the same reasons. The respondents who saw Experiment 2 were asked to
imagine a situation in which they need to replace their refrigerator. Among two
refrigerators, they were asked to identify the refrigerator with the lowest lifetime cost.
The two appliances differed only in terms of their purchase price, their energy
consumption, and the energy efficiency rating (A+++ versus A+). The remaining
characteristics of the two refrigerators were identical. The information was presented in
the same way as it is presented in the current version of the EU energy label for
refrigerators (see Fig. 2).13 The participants were randomly assigned to one of two
different treatments. In Treatment 1, the information on yearly energy consumption of the
two appliances was displayed in terms of physical consumption (kWh), as it is displayed in
the current version of the EU energy label (see Fig. 2). In Treatment 2, the information
on electricity consumption was displayed in monetary terms, i.e. in the form of an
estimate of the yearly energy cost. As mentioned, we controlled for order effects by
randomly changing the order of the two refrigerators in both treatments. In both
experiments, also the order of the answer options was randomized in order to control for
order effects in the presentation of the answer options.14 Respondents were asked which of
the two refrigerators would minimize their expenditure on the cooling of food and
beverages during 10 years of planned usage. Again, the question was not about the
respondent's subjective preference for either the one or the other refrigerator, but about
which of the two appliances creates less lifetime costs. In Experiment 2, at the Swiss
average electricity price of 20 Rp. /kWh, the 100 kWh more energy-efficient refrigerator
has an annual energy cost of CHF 20 compared to that of CHF 40 for the 200 kWh
refrigerator (Fig. 2). Over 10 years of planned usage, the total energy costs (in the
absence of discounting) are CHF 200 and CHF 400 respectively, which from the private
perspective does not justify the difference of CHF 500 in the upfront purchase prices. The
less energy-efficient refrigerator is hence minimizing the total lifetime costs.15 While
the general setup was very similar in both experiments, it has to be highlighted that they
also differed in a decisive way: While in Experiment 1 the more energy-efficient bulb was
also the one that minimizes lifetime cost, Experiment 2 was designed in a way that the
refrigerator with the lower energy consumption, i.e. the more energy-efficient appliance,
was not the appliance that minimized lifetime cost. This seems counter-intuitive, as in
such a case an ‘energy-efficiency gap’ does not exist. It is perfectly rational for the
consumer to choose the less efficient appliance, at least from a private perspective. The
reason why this specific setting was chosen was to identify those individuals who
performed an investment analysis and to distinguish them from the respondents who followed
a heuristic decision-making strategy. If the more expensive (and more energy-efficient)
appliance would have had the lowest lifetime cost, individuals applying a decision
heuristic (such as choosing based on the energy-efficiency rating provided on the energy
label) would have ended up making the same choice as the ones who performed an investment
analysis. This would not allow to discriminate between the two groups of decision-makers.
In a debriefing question after the choice task, respondents were asked about the decision-
making strategy they had adopted when making their choice. Several decision making
strategies were offered: one being performing an investment analysis (comparison of
lifetime cost) and the other being heuristic decision-making strategies such as comparing
the purchasing prices of the two products, comparing the yearly electricity consumption,
comparing the energy-efficiency ratings on the labels or making a random choice. The light
bulb experiment also had another strategy choice to compare based on the lifetime of the
two bulbs. An open answer option “Other reason” was also provided (Fig. 5 in the
appendix). Answer options were again randomized to control for order effects. The
introduction of this debriefing question gives us the possibility to econometrically
analyze the factors that influence the choice to perform an investment analysis, and,
therefore, to adopt a rational decision strategy. However, it has to be noticed that in
Experiment 2, among all respondents who claimed to have performed an investment analysis
as their decision strategy, almost 37% incorrectly selected the more costly fridge as the
most (cost-)efficient appliance (in Experiment 1, the number of such cases was about
5.1%). There are two possible explanations for this: either the calculation was not
performed correctly or the self-reported decision-making strategy does not necessarily
coincide with the actual strategy applied. In Experiment 1, about 28.0% of the respondents
claimed to have compared the electricity consumption of the two light bulbs. About 22.9%
mentioned that they made an investment calculation before making the choice. Another 24.4%
of the respondents reported to have compared the energy-efficiency ratings on the label
and 13.0% said they made their choice based on the lifetime of the two bulbs. 2.9%
answered that they had compared the purchase prices of the two bulbs and another 7.6% of
the respondents either mention other reasons for their choice or report that they made a
rather random choice. In Experiment 2, most of the respondents self-reported that they
compared the energy-efficiency ratings on the energy labels (45.2% of respondents). 27.7%
of the respondents claimed to have compared the electricity consumption of the two
refrigerators, and 17.6% claimed that they made an investment calculation to evaluate the
two appliances. Only 1.9% of respondents reported to have compared the purchasing prices,
3.0% indicated that they made a rather random choice and 3.5% stated that they had other
reasons for their decision.16 Table 2 gives a summary on how the respondents were
distributed as the two treatment groups, and also their responses for the two outcomes of
focus in this study: the choice of investment analysis as their decision strategy, and the
correct identification of the cost-efficient household appliance. In addition to the
randomized controlled experiment, the questionnaire included several other questions
related to the household's energy consumption as well as questions on sociodemographics of
the respondent and other household members. We included information on respondents’ age,
gender and level of education, their attitudes towards energy conservation as well as
their energy and investment literacy, which is used in the econometric analysis. The
gender is represented by a binary variable (FEMALE) which takes value one if the
respondent is female. Age of the respondent is captured through three binary variables
representing age groups – less than 40 years (AGE40M as reference category), between 40–60
years (AGE40_69) and 60 years or above (AGE60P). The ownership status of the residence
(owned or rented) is captured via a binary variable (OWNER) that takes value one if the
residence is owned by either the respondent or another member of the household. Monthly
gross household income is captured through three binary variables representing income
groups –less than CHF 6′000 (HHI6K as reference category), between CHF 6′000 – CHF 12′000
(HHI6_12K) and more than CHF 12′000 (HHI12K).17. The binary variable UNIEDU takes value
one if the respondent holds a university degree. The survey language in which the
respondent has taken the survey is also accounted for. The dummy variable ITALSP is 1 for
survey taken in Italian (applies to the light bulb experiment) and the dummy variable
FRENCHSP is 1 for survey taken in French (applies to fridge experiment). All econometric
specifications also control for the respondents’ level of energy literacy and investment
literacy. Energy literacy is measured by an index (ENLIT_IN) that accounts for several
dimensions of energy-related knowledge. This index ranges from 0 to 11 and is based on
correct responses to several questions that examine (i) knowledge of the average price of
a kilowatt hour of electricity in Switzerland; (ii) knowledge of the usage cost of
different household appliances; and (iii) knowledge of the electricity consumption of
various household appliances. Investment literacy is measured by a binary variable
(INVLIT) that takes the value one if the respondent correctly solved a compound interest
rate calculation.18 Compound interest rate calculations are usually used to assess an
individual's financial literacy (Lusardi and Mitchell, 2007, 2009; Brown and Graf, 2013).
Furthermore, we account for the individual's pro-environmental moral attitude (ATTMORAL)
and their concern for free-riding (ATTCONCE) by asking for agreement or disagreement to
two statements on a 5-point likert scale. The two statements are “I feel morally obliged
to reduce my energy consumption” and “I am not willing to reduce my energy consumption if
others don’t do the same”. Each of the two binary variables takes the value one if the
respondent chooses ‘agree’ or ‘strongly agree’. Lastly, all specifications control for the
treatment effects of displaying the yearly electricity consumption in monetary terms
(binary variable TREATCHF), as well as for any effect of the order in which the two
appliances are presented (binary variable ORDEFF). An overview of the summary statistics
for the variables used in our econometric models for Experiment 1 and Experiment 2 is
presented in Table 3. The two samples are found to be similar in terms of ownership, share
of higher income households, share of respondents with university education and their
attitudes towards environment. The sample in the refrigerator experiment has a larger
share of old population than in the light bulb experiment. It also has a higher share of
female respondents and low income households. The sample in Experiment 1 appears to have a
higher energy-related literacy as well as investment literacy. We also notice that about
23% of respondents in the Experiment 1 employ investment calculation as their decision
strategy compared to 18% in the Experiment 2. Unsurprisingly, due to the experimental
design, most of the respondents in the light bulb experiment are able to correctly
identify the most cost-efficient light bulb. In the refrigerator experiment though, only 1
in 5 respondents correctly identifies the most cost-efficient refrigerator.

<h>EMPIRICAL MODEL</h>
---------------

The data collected from the survey and from the two experiments allows us to analyze the
impact of the display of monetary information about future energy consumption as well as
the level of energy and investment literacy on the ability to identify the light bulb and
refrigerator with lowest lifetime cost. Further, the debriefing question about the
decision making strategy gives us the possibility to analyze the factors that influence
the choice to perform an investment analysis. Therefore, from the econometric point of
view, we are interested in explaining the impact of information, energy and investment
literacy and other socioeconomic factors on two binary outcome variables. In one case, the
dependent variable takes the value 1 if someone chose the most cost-efficient appliance
and 0 otherwise. In the second case when analyzing the decision strategy, the outcome
variable takes the value 1 if someone chose to perform an investment calculation and 0
otherwise. From a methodological point of view, such binary outcome variables are the
simplest case of a discrete choice situation and can for example be analyzed using a
probit model (Greene, 2003). The separate estimation of two single equation probit models
described above is based on the assumption that the two outcome variables can be
independently determined. This may or may not hold true in reality. We believe in our
context it can be safely assumed that the two outcome variables should be determined
jointly rather than individually. In this case, from an econometric point of view, a
bivariate probit model could be applied for a simultaneous estimation of the two binary
outcome variables. Furthermore, even more precisely, the ability to identify the most
cost-efficient appliances could be modeled as a two stage decision process, explaining
first the choice to adopt a decision strategy based on an investment calculation, and then
the identification of the cost efficient appliance. In this case, an appropriate
econometric model for this sequential decision-making process is the recursive bivariate
probit as it accounts for the likely endogeneity of the investment calculation variable in
the equation related to the identification of the cost efficient appliance.20 Most of the
following discussions and results refer to the recursive bivariate probit model, which is
our preferred model. Nevertheless, in this paper we still decided to estimate two separate
probit models and a bivariate probit model for each of the two experiments for comparison
purposes. The exogenous variables in the model comprise socioeconomic characteristics of
the respondent (age, sex and university education) and that of the household (household
income and if the residence is owned or rented); environment related attitudes; the level
of energy and financial literacy of the respondent; the treatment variable (i.e. yearly
electricity consumption shown in physical or monetary units) and some other variables like
language in which the survey was taken and the order in which the two appliance choices
were presented. It is important to note that the model is identified irrespective of
whether the exogenous variables x1 and x2 in the two equations are different or not.21
Moreover, such a recursive model of simultaneous equation can be estimated using the full
information maximum likelihood (FIML) approach ignoring the simultaneity.22 In a non-
linear model, marginal effects are more informative than coefficients, because they inform
us how the outcome variable will change when an explanatory variable changes. The marginal
effects can be calculated for each observation i or for any specific vector of the
regressors. In this study, the marginal effects are calculated for the sample mean. The
expression for the marginal effects23 could be derived following Greene (1998) and Kassouf
and Hoffmann (2006). For a two equation model, one would obtain a direct effect for
variables appearing on the right hand-side of the choice equation (i.e. x2) and an
indirect effect for explanatory variables in the decision strategy equation (i.e. x1). The
indirect effect on the correct choice occurs via the endogenous decision strategy variable
which also appears on the right-hand side of the choice equation. The total effect is then
the sum of the direct and the indirect effects. Similarly, the effect of an exogenous
continuous variable (say z) is calculated by computing the partial derivative of the
unconditional mean function in Eq. (13) with respect to z. The somewhat complicated
expression appears in Kassouf and Hoffmann (2006, p. 115) and the analysis appears more
generally in Greene (1996, 1998). We are interested in calculating the impact of at least
four variables of interest on the choice of decision strategy and in turn on the correct
choice of the (cost-)efficient appliance — energy literacy, investment literacy, monetary
treatment and the endogenous decision strategy to make an investment analysis. We have
used NLOGIT for the model estimation and calculation of the marginal effects presented in
this paper.24

<h>RESULTS</h>
-------

Below we present the estimation results for our two online randomized controlled trials.
Three probit models were estimated for each of the two experiments for comparison purpose
— the single equation probit (Probit), bivariate probit (Biv. Probit) and the recursive
bivariate probit (Rec. Biv. Probit).25 These models give us insights into the factors that
influence the decision strategy and the identification of the appliance that minimizes
total cost over the entire lifetime. Table 4 presents the empirical results from
Experiment 1. Following this, Table 5 shows the results from Experiment 2. Finally we
compare the results across the two experiments and present the estimated marginal effects
for our quantities of interest, i.e. energy literacy, investment literacy, monetary
treatment and investment analysis strategy on the identification of the cost-efficient
appliances.26

<hs>  Empirical results</hs>
  ~~~~~~~~~~~~~~~~~

Table 4 shows results of the three model specifications for the light bulb experiment. The
slope coefficients in Table 4 are quite similar for the investment calculation equation
across the three models. Differences are apparent in the appliance choice equation,
particularly when comparing the first two models to the recursive bivariate probit. The
correlation coefficient (ρ, shown as RHO(1,2) in the table) between the two error terms is
significant only in the recursive bivariate setting. Limiting the discussion to the
recursive model which is our preferred framework, we observe a significant negative effect
of gender and age (AGE60P) on choosing an investment analysis approach, and in turn on the
identification of the cost-efficient appliance. University education, energy and
investment literacy, and TREATCHF (i.e. getting the energy consumption information in
monetary terms) – all appear to have a significant positive effect on the decision to
perform an investment calculation. In the appliance choice equation, AGE60P has a
significant and positive slope coefficient likely due to the fact that older respondents
could have identified the cost-efficient light bulb via several other decision heuristics.
Furthermore, the coefficient on INVCALC is significantly positive which signifies a
positive impact of choosing an optimization decision strategy on the probability to
identify the cost-efficient appliance. Table 5 shows the results from Experiment 2, the
fridge experiment. The coefficients appear similar for the investment calculation equation
across the three models and most of the significant effects are also more prominent in
magnitude. Higher income levels are seen to be positively associated with the correct
identification of the cost-efficient refrigerator in the probit and biprobit settings. The
correlation coefficient is significant in both the bivariate and the recursive bivariate
setting. We notice that most effects are stronger in Experiment 2, likely due to the fact
that making a correct investment calculation was a necessary strategy to identify the
cost-efficient refrigerator. Within the recursive bivariate framework, we again find a
significant negative effect of gender and age (AGE60P) on choosing an investment analysis
strategy. University education has a positive effect. Energy literacy shows a significant
positive effect in both equations. Investment literacy and monetary treatment both show a
very strong effect on the decision to perform an investment calculation. TREATCHF also has
a significant effect in the appliance choice equation now. Moreover, the coefficient on
INVCALC is strong and significant highlighting the role of choosing an optimization
decision strategy on the identification decision of the cost-efficient refrigerator.
Summarizing the most important findings: We observe a positive and significant effect of
energy literacy (ENLIT_IN) and investment literacy (INVLIT) on the choice of investment
calculation as the decision strategy in both experiments. This supports Hypothesis H1a in
that individuals with a higher cognitive ability are more likely to follow an optimization
strategy rather than a heuristic strategy. Furthermore, the coefficient on INVCALC is
significantly positive which signifies a positive impact of choosing an optimization
decision strategy on the appliance choice step, which in turn supports Hypothesis H2a. All
these effects are in particular found to be stronger in Experiment 2, wherein making an
investment calculation was a necessary strategy to identify the cost-efficient appliance.
The effect of being in the treatment with monetary information on yearly electricity
consumption is strong and highly significant in almost all model specifications thereby
supporting Hypotheses H1b and H2b. As expected, the treatment effects are again stronger
in the fridge experiment. No significant order effect is found in either experiment which
indicates the absence of any bias due to the order of the presented appliance choices.

<hs>  Marginal effects</hs>
  ~~~~~~~~~~~~~~~~

In Table 6, we present the marginal effects at the sample means for the variables that are
particularly important to verify our hypotheses. The marginal effects are computed for the
two variables measuring energy and investment literacy, the dummy variable capturing the
treatment effect of displaying yearly energy consumption in monetary terms, as well as the
endogenous dummy variable of choosing an investment analysis decision strategy. We
restrict the discussion to the reported results from our preferred model, which is the
recursive bivariate probit. It is shown that the fact that an individual is able to do
complex calculations increases the probability to choose the most cost-efficient appliance
by 2–3 percentage points in Experiment 1 and by about 19–20 percentage points in
Experiment 2. Similarly, an increase in an individual's energy literacy score (measured on
a scale of 0 to 11) also increases the probability to choose the most cost-efficient
appliance. The higher marginal effect in Experiment 2 (3 percentage points) is likely due
to the fact that in this experiment, the most cost-efficient appliance could only be
identified when comparing lifetime usage costs of both appliances, which requires some
calculation. In Experiment 1, also the comparison of the power of the two light bulbs,
their lifetime or the comparison of the energy-efficiency rating on the label lead to the
choice of the most cost-efficient appliance. Hence, the ability to make complex
calculations was less important here. For the same reason, also the marginal effects of
providing the yearly energy consumption in monetary terms rather than physical units are
much higher for Experiment 2. While the probability to choose the most cost-efficient
light bulb increased by about 4 percentage points when the monetary information was
displayed in the light bulb experiment, the probability increased by about 30 percentage
points in the case of the refrigerator experiment. This result gives strong support for
Hypotheses H1b and H2b, i.e. that the information on yearly energy costs strongly
increases the chances that consumers choose the more (cost-)efficient appliance. Lastly,
the marginal effect of the endogenous investment calculation decision strategy variable is
up to 8 percentage points in Experiment 1 and up to 78 percentage points in Experiment 2.
The strong impact supports our Hypothesis H2a that opting for optimization as the
decision-making strategy has a positive impact on the probability to identify the most
cost-efficient appliance.

<h>CONCLUSION</h>
----------

In order to examine the role of information display, energy and investment literacy on the
choice of electrical appliances of consumers, we have organized a household survey and
conducted two online randomized controlled trials among households from three major Swiss
urban areas. The first experiment was related to a choice between two light bulbs whereas
the second experiment was concerned with making a choice between two refrigerators. The
information collected from the survey was analyzed by estimating a series of (recursive)
bivariate probit models in order to simultaneously model two binary variables which
represent the two stage decision process explaining first the adoption of the decision
strategy and then the identification of the cost-efficient appliance. From the survey we
observe that more than two-third of the consumers do not perform an investment
calculation, which supports the view that a large part of the consumers are boundedly
rational and prefer to use shortcuts instead of optimizing their expenditure. Further,
from the econometric analysis we observe that displaying yearly energy consumption of
appliances in estimated yearly energy cost rather than in physical units increases both
the probability that consumers perform an investment analysis and that they identify the
most (cost-)efficient appliances. Our results emphasize that informed and rational choices
of appliances can be enhanced by the provision of monetary information on yearly energy
consumption. Furthermore, we could show that individuals who possess energy-related
knowledge and high cognitive abilities, captured by high levels of energy and investment
literacy, were more likely to opt for optimization as the decision-making strategy which
in turn positively influences the probability to identify the most cost-efficient
appliance. It can therefore be concluded, that enhancing an individual's energy-related
knowledge and the ability to make complex (investment) calculations seems to be one
important prerequisite to empower consumers to make rational and informed energy-related
choices. From an energy policy point of view, the results suggest that an improvement in
energy efficiency could be reached in three ways. First, with an obligation for the
producers of electrical appliances to provide information on the future energy consumption
of the product in the form of a monetary estimate. This could follow the example of the
EnergyGuide label used in the United States that requires that on certain appliances an
estimate of the annual operating energy cost is displayed (US-FTC, 2017). A second
strategy would be to educate consumers about the energy consumption of different
appliances and how to identify the most efficient appliances by means of brochures and
energy literacy courses at schools. As a third strategy, decision support tools such as
lifetime-cost-calculators could be provided in stores, mobile applications or through a
web-page promoted by the government. All these measures would make use of the insights
that energy and investment literacy as well as the display of monetary information seem to
improve individual decisions when it comes to the identification of efficient household
appliances.


<h>REFERENCES</h>
----------

  [1] Hunt Allcott, Michael Greenstone. Is there an energy efficiency gap?. doi:10.1257/jep.26.1.3
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<ART>Business capital accumulation and the user cost: Is there a heterogeneity bias?
===============================================================================

Authors: Serena Fatica
DOI: 10.1016/j.jmacro.2017.12.004
Year: 2018  |  Pages: 15-34
ASJC codes: 2002
Keywords: Capital accumulation, Corporate taxation, Panel data, User cost of capital

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Using data from 23 sectors in 10 OECD countries over the period 1984–2007 we show that the homogeneity assumption underlying empirical models of capital accumulation may lead to mis-specification. Thus, we adopt a fully disaggregated approach – by asset types and sectors – to estimate the responsiveness of investment to the tax-adjusted user cost of capital. Once all the sources of heterogeneity are accounted for, we find that capital accumulation is significantly affected by changes in the user cost, although the size of the impact is smaller than the unit benchmark. We do not find robust evidence that the long run substitution elasticities are statistically different across asset types.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Capital accumulation is crucial for business cycles and economic growth. Understanding its
drivers is therefore essential. Among the potential determinants, the literature has
extensively investigated the role of the user cost (see Chirinko (1993a, 2008) for
comprehensive surveys). Most studies treat capital as a homogeneous good. However, there
is motivated concern that the single capital good model inadequately describes the effects
of changes in the user cost on capital accumulation, primarily because it neglects
compositional shifts in investment. In fact, different capital goods command different
prices, display different depreciation patterns, and receive a specific tax treatment.
First, market prices vary widely across assets and over time. In some cases, price changes
might reflect long-term trends, such as technological progress. For instance, quality
improvements in high-tech components have led to a dramatic decline in market prices for
computers and similar goods (Greenwood et al., 1997). Secondly, technological features
directly affect adjustment costs, which presumably increase with the useful life of the
assets. Likewise, the durability of capital goods determines the amount of replacement
investment needed to sustain a given level of production, under unchanged technological
constraints. Thirdly, the impact of tax policy differs across capital asset types. Tax
allowances for depreciation of capital expenditure are typically asset–specific, or
defined for relatively narrow asset categories (Clark, 1993; House and Shapiro, 2008).
Moreover, even non-targeted tax policy measures translate into different relative changes
of the user cost of different assets, depending on its initial level (Cummins et al.,
1996). Importantly, both asset and sector specificities matter for the trajectories of
capital accumulation. In so far as different sectors are technologically constrained to
rely on specific capital assets, investment evolves unevenly across industries. The
responsiveness to cost variables changes also if supply is rigid and if the capital assets
are not easily redeployable, even within sectors (Goolsbee, 1998). Moreover, increased
asset specialization, by reducing the incentives for disinvestment, might alter the
sensitivity of investment to its cost. As Desai and Goolsbee (2004) point out, these types
of irreversibilities are likely to manifest at the microeconomic level – i.e. at the level
of the individual asset and sector – “rather than apply to all assets in all sectors
homogeneously” . Abandoning the assumption of homogeneous capital creates challenges for
investment modelling. In the context of structural models, the combination of different
types of capital goods into a single aggregate imposes unappealing restrictions, on either
the level and the shape of adjustment costs (Wildasin, 1984; Chirinko, 1993b), or the
degree of substitutability among assets (Hayashi and Inoue, 1991). On the empirical side,
aggregation creates issues for the construction and measurement of variables in the first
place. Moreover, naturally, econometric models with aggregate variables force homogeneity
on the estimated parameters. Likewise, the standard panel data pooled estimators constrain
the slopes in the estimating equation to be the same across cross-section units. This
might have severe consequences in reduced-form models of capital accumulation resting on
the long run cointegrating relationship between the actual and the frictionless level of
capital implied by economic theory (Caballero et al., 1995). In this paper, we investigate
the consequences of imposing homogeneity when estimating the sensitivity of investment to
the tax-adjusted user cost of capital. We use data – including detailed information on
business tax incentives – for 23 sectors comprising the market economy in 10 OECD
countries over the period 1984–2007. Our setup accommodates heterogeneity across capital
asset types and economic sectors. As such, it departs from the bulk of the literature on
the substitution elasticity, based on aggregate data (Schaller, 2006; Caballero, 1997;
Bond and Xing, 2015). In focusing on asset heterogeneity we take inspiration from Tevlin
and Whelan (2003), who reveal the shortcomings of aggregate models due to the rising
importance of computers as of the 1990 s in the US. Smith (2008) and Bakhshi et al. (2003)
provide similar analyses for the UK. We extend their contributions not only by considering
a broader set of assets, countries and sectors, but also by systematically investigating
the effects of neglected heterogeneity along these dimensions. Our paper also relates to
the recent article by Bond and Xing (2015). They use the same investment data (although a
slightly different sample definition) as we do, but still work with aggregate measures of
capital. We show that their conclusions do not necessarily survive a finer definition of
capital goods. Moreover, we formally examine how heterogeneity affects econometric
estimates of the substitution elasticity, something that is inherently different from the
focus of their analysis. The remainder of the paper proceeds as follows. Section 2
discusses a way to deal with multiple capital assets in a standard empirical investment
model. Section 3 introduces the data, and some stylized facts. Section 4 describes our
empirical strategy. The results are in section 5. Finally, section 6 offers some
concluding remarks.

<h>INVESTMENT MODEL: THEORETICAL BACKGROUND AND EMPIRICAL SPECIFICATION</h>
--------------------------------------------------------------------

The two capital series need not be equal on average, as they can differ up to a stationary
error term, e, which captures transitory deviations. In our framework, for a single
cointegrating relationship to exist, the capital output ratio and the user cost must be
cointegrated. In turn, this imposes constant returns to scale on the production
technology, which we assume throughout as in Caballero (1997). Precisely relying on the
cointegration between the two capital series, the full specification with short run
dynamics can be reparametrized into an error correction model (ECM), as in Bloom et al.
(2007). We discuss the empirical implementation of the ECM in Section 4, and now turn to
the issue of heterogeneity and aggregation. Aggregation over heterogeneous capital goods
creates analogous econometric issues. In the first place, one should ensure consistency
between the aggregate measures of quantities and cost variables (Bakhshi et al., 2003). In
practice, capital stock series available from the national accounts are obtained
additively from the individual series. The corresponding tax-adjusted user cost is built
as an aggregate quantity-weighted index of the asset-specific user costs. Fitting an
equation for investment requires that, for consistency, the aggregate user cost be built
as a price index for investment, though. Thus, the sets of weights will differ unless all
capital assets accumulate in proportion to their stock value.3 Even with appropriately
defined asset weights, aggregation of the non-price component of the user cost may still
be problematic, as it would propagate any measurement errors affecting the tax terms of
the single capital assets (Goolsbee, 2000). Overall, the discussion above casts doubt on
the fact that ignoring heterogeneity would lead to correctly specified empirical models of
capital accumulation. To deal with cross-sectional heterogeneity, we analyze the dynamics
of the different capital goods separately and use estimators that allow for heterogeneous
parameters. With our data, we can factor in heterogeneity down to the country-sector
level.4

<hs>  Variables and main sources</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~

Our dataset includes 23 sectors (SIC 2-digit classification) adding up to the market
economy of 10 OECD economies over the period 1984–2007. Overall, this gives a panel of up
to 5060 observations, for 230 country-sector pairs. Details on the sample coverage are
reported in Appendix A. Data on production are taken from the EU KLEMS database, which
provides harmonized series for capital stock and output at the sector level for European
and other advanced economies (O’ Mahony and Timmer, 2009) .5 The stock of fixed capital in
the KLEMS data breaks down into several asset types. We focus on the following: computers,
communication equipment, transportation equipment, and other machinery and equipment.
These assets make up aggregate equipment capital. Adding up structures gives the overall
stock of productive physical capital used in the market economy.6 The capital stock series
(with 1995 as the base year) are obtained using the Perpetual Inventory method by summing
up past real investments, weighted by the relative efficiencies of capital goods at
different vintages. Asset-specific depreciation rates are equal across countries and time,
but can vary across sectors. They are lowest for structures (the minimum rate is around
2%). When it comes to equipment capital, depreciation rates range from 9% for
transportation equipment, to 31.5% for computers. Wear and tear for the different capital
aggregates is determined endogenously by the relative importance of the different assets.
Average depreciation rates for total capital and equipment are 8% and 14%, respectively,
over the sample period. Thus, average values hide significant cross-sectional differences
across asset types. Variation along the time-series dimension is equally important. The
average economic depreciation rate for total capital increases from 7% to almost 10% over
the sample period, while the rate for equipment capital rises from 13% to 16%. This is a
result of the dramatic increase in the use of rapidly depreciating equipment capital (see
next section). Asset-specific price indices for gross fixed capital formation are also
available at the sector-country pair level. The base year for the price indices is 1995.
We use value added as a measure of sector output. The corresponding deflator is also taken
from the KLEMS database. When it comes to the non-price component of the user cost of
capital, the main source for the tax rules is ZEW (2013), which provides disaggregated
data by asset and sector according to the KLEMS classification. To fill the gap of missing
information in the earlier years of our sample, we have used the International Bureau of
Fiscal Documentation (IBFD) and the International Tax Summaries by Coopers and Lybrand.
Profit taxes are measured by the headline statutory tax rates on corporate income,
augmented by local taxes and surcharges, potentially sector-specific sectors, whenever
applicable. Importantly, provisions on tax depreciation allowances and other incentives,
such as accelerated depreciation, are also asset-specific. When there are multiple rules
under national tax codes, the most efficient scheme is applied. The real discount rate is
calculated as the opportunity cost of finance, namely as a weighted average of the cost of
equity and the cost of debt, net of CPI inflation. Details on the calculations of the user
cost are in Appendix B.

<hs>  Stylized facts</hs>
  ~~~~~~~~~~~~~~

Here we illustrate some key features of the data, which further motivate our preference
for a disaggregated approach in modelling investment demand. Fig. 1 plots the capital-
output ratio and the user cost of capital for both the aggregate capital stock and
equipment capital. The overall capital-output ratio decreases slightly over the sample
period. At the same time, the series for equipment capital appears clearly rising as of
the mid-1990s, while being relatively flat previously. Taken together, this evidence
points to a compositional shift within physical capital. In particular, the increased use
of aggregate equipment is accompanied by a decreased importance of structures, which
ultimately drives down the aggregate capital-output ratio. The user cost of capital shows
a clear downward trend, with the reduction especially marked in the case of aggregate
equipment. Fig. 2 depicts the evolution of quantities and prices for disaggregated capital
series. There is a clear declining trend in the use of structures (Panel A, left hand
side). Likewise, aggregation hides diverging dynamics also within aggregate equipment
capital, where a compositional shift towards short-lived high-tech capital assets is
apparent. At the same time, other machinery and equipment shows a strong downward trend
over the sample period (Panel B, left hand side). Fig. 2 (right hand side column) plots
the calculated tax-adjusted user cost of capital for the disaggregated asset series.
Again, IT capital assets display similar patterns, with a downward trending user cost,
particularly for computers. On the contrary, the user cost of transportation equipment and
other machinery and equipment do not show overall clear trends, but rather upward and
downward dynamics over shorter sub-periods. The same holds for the user cost of structures
(panel A). In logs, the user cost can be expressed as the sum of two components: the
relative price of capital and the non-price component, which comprises the cost of
finance, the tax term, and the depreciation rate. Fig. 3 depicts the evolution of the
relative market price and of the tax term for each of the five assets. As a mirror image
of the large rise in volumes, relative prices of both computers and communication
equipment (averaged across country-sector pairs) display pronounced negative trends. This
is a well-known fact, often taken as evidence of quality improvements stemming from
investment-specific technological change (Greenwood et al., 1997). By contrast, the market
price for structures is trending upwards, while the relative prices of transportation
equipment and other machinery are relatively flat. The tax term of the user cost displays
far less heterogeneity across capital assets than the price component (right hand side of
Fig. 3). The significant reduction in statutory tax rates on corporate income across OECD
countries seemingly lies behind the generalized downward trend observed for the tax term.
Short run dynamics are somewhat more volatile, being most likely driven by changes in the
asset-specific depreciation allowances. So far we have focused on the dynamic properties
of quantities and prices. Taking a look at the cross-sectional variation in the allocation
of the capital assets is also useful, as this would give an indication on the degree of
heterogeneity in the underlying production technologies across sectors and countries. In
Fig. 4 we present box plots for the shares of each capital type into the stock of total
capital across sector-country pairs in 2007. Expectedly, structures and other machinery
and equipment show the largest median shares. In general, the interquartile range of
shares is relatively narrow with respect to the tails of the respective distributions.
Moreover, there are quite a few outliers for all assets the short-lived assets.

<h>ECONOMETRIC MODELLING</h>
---------------------

In addition to coefficient heterogeneity, another important source of concern in
estimation is the presence of cross-sectional dependence in the error term due to omitted
common factors. Common correlations can arise from macroeconomic shocks affecting all the
sectors. Moreover, in our setup, sectoral linkages imply that shocks that are specific to
capital-producing sectors propagate throughout the rest of the economy (Foerster et al.,
2011). Such interlinkages in the use of capital inputs may effectively transform
idiosyncratic shocks into common shocks. While the strength of the amplification mechanism
depends on the structure of production linkages between sectors (Horvath, 1998), the scope
for transmission clearly increases when an aggregate measure of capital is considered.
Common shocks can induce cross-sectional dependence in the residual, and, if correlated
with the regressors, result into inconsistent estimates. Likewise, correlation across
cross-section units may also lead to significant size distortions in panel unit root tests
that assume independence. However, if the extent of cross-sectional dependence of errors
is sufficiently weak, or limited to a small number of units, then its consequences in a
standard setup are negligible (Chudik and Pesaran, 2014). While the conventional pooled
estimators control for the presence of unobserved common factors with the time fixed
effects, relaxing the slope homogeneity restriction calls for alternative strategies to
deal with such unobservables.10 Specifically, we first implement the Mean Group estimator
on cross-sectionally demeaned variables (CDMG), viz., variables measured as deviation from
their year-specific average over the whole sample. This procedure eliminates trending
components that are common to all sector-country pairs, and thus allows one to deal with
common factors affecting capital accumulation, although only imperfectly when slopes are
heterogeneous. By augmenting the estimating equations with country-sector specific linear
trends we control for group-specific shocks that evolve linearly over time.

<hs>  Time series properties</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

Since the error correction specification rests on the cointegration between the
frictionless capital and the actual level of capital, it is important to investigate the
time series properties of the variables. To this end, we employ the panel unit root test
proposed by Pesaran (2007), which allows for heterogeneity and cross-sectional
correlation.11 We run the test for up to three lags, and found that in general the
quantity and price variables are non- stationary in levels, both for the raw and the
demeaned series. The detailed results are in Appendix C.

<hs>  Investment equations</hs>
  ~~~~~~~~~~~~~~~~~~~~

We estimate Eq. (9) on both aggregate measures of capital and disaggregated asset types.
Our composite variables are total capital and aggregate equipment, which differ only
because of the inclusion of structures into the former aggregate.12 Subsequently, we split
aggregate equipment into its components – computers, communication equipment,
transportation equipment and other machinery and equipment. In all cases, we apply the
different panel techniques discussed in Section 4. As an extension, we then allow the
price and the non-price components of the user cost to have different long run impacts on
capital accumulation. Further, we estimate the model for a debt-financed investment. In
discussing the estimated coefficients, we focus on the adjustment coefficients and the
implied long run substitution elasticity. To put our results in perspective and facilitate
comparison with the literature, we test if the substitution elasticity is statistically
different from one, the value of the Cobb-Douglas production function. More importantly
for our purposes, we also test if the elasticities are equal across asset categories.13 In
this way, we can assess whether and to what extent the types of capital respond
differently to the price variable. We also perform diagnostic tests for residual
stationarity - again using the test proposed by Pesaran (2007) -, and for the presence of
cross-sectional correlation (Pesaran, 2004) .14 The root mean squared error (RMSE)
statistic is reported as a measure of goodness of fit.

     <hss>Aggregate capital</hss>

        We first estimate the error correction model for total capital and aggregate
        equipment using the standard two-way fixed effects (2FE) estimator and the MG
        estimators. The regression results are in Table 1. First, let us look at the
        models with homogeneous parameters (first and fourth column, respectively). The
        short run coefficients are all consistent with the underlying theory and
        significantly different from zero. The point estimates of φ suggest that the speed
        of adjustment towards the long-run target level is somewhat slower for total
        capital than for aggregate equipment. This is consistent with previous evidence
        pointing to a significantly sluggish adjustment of structures (Desai and Goolsbee,
        2004; Schaller, 2006). The implied long run substitution elasticity for total
        capital is statistically different from one at conventional significance levels,
        whereas the case for rejecting the Cobb-Douglas benchmark is not equally
        compelling for equipment capital alone. The estimated elasticities are in the
        upper range of the literature results, in line with studies using firm-level data,
        such as Cummins et al. (1996), Schaller (2006), and Caballero et al. (1995). The
        Wald test rejects the hypothesis of equal long run elasticities at 5% level
        (p-value of 0.012). Residual diagnostics reveal the presence of strong cross-
        sectional dependence. Moreover, the residuals in the equation for aggregate
        equipment appear non-stationary, which casts doubt on the validity of the
        inference drawn for that specification. Allowing for heterogeneous parameters with
        demeaned variables (second and fifth column in Table 1) results into a faster
        speed of adjustment and decreased long-run elasticities (in absolute value). In
        particular, the coefficients are half in size compared to the 2FE estimates. The
        test for a unit long-run elasticity is rejected for both capital aggregates.
        Moreover, the Wald test does not reject the hypothesis that the long-run
        elasticities for the two capital series are equal. While the residuals in both
        equations appear stationary, demeaning does not alleviate the problem of strong
        cross-sectional dependence. The estimates from the CCE version of the Mean Group
        model (third and sixth column) point to long-run elasticities centered on 0.4
        rather than one. These results broadly corroborate the findings in Bond and Xing
        (2015), who estimate elasticities for total capital between −0.5 and −0.3, values
        within the range of previous findings (Smith, 2008). Again, we cannot reject the
        hypothesis that the elasticities are statistically equal at conventional
        significance levels. Importantly, the residuals from the model are well behaved,
        as they are stationary and reveal only weak cross-sectional dependence.

     <hss>Disaggregated capital</hss>

        We estimate the error correction model in Eq. (9) separately for structures and
        for the different equipment types – computers, communication equipment,
        transportation equipment, and other machinery and equipment. We start from the
        standard 2FE pooled model, and then implement the Mean Group approach. The results
        are reported in Table 2 and 3, respectively. The speed of adjustment of the
        capital series to their long-run targets is faster for computers than for other
        types of equipment, while structures exhibit, expectedly, a sluggish behavior. The
        long-run substitution elasticity is not statistically different from one in the
        case of IT capital (computers and communication equipment) and, marginally,
        transportation equipment. Structures and other machinery and equipment display
        much lower elasticities (in absolute value), but still statistically significant
        (see Table 2). The findings are consistent with previous evidence pointing to a
        relatively high responsiveness of short-lived capital, particularly computers
        (Tevlin and Whelan, 2003) compared to slowly depreciating assets (Bakhshi et al.,
        2003). Residual inspection for the different types of equipment does not give
        fully reassuring results when it comes to stationarity, however. Strong cross-
        sectional dependence is also an issue for all asset types, except computers. We
        interpret this result as evidence of the different nature of the unobservable
        common shocks hitting the different capital goods. Specifically, in the case of
        computing equipment the shocks seem common to sectors and countries. This is fully
        consistent with supply side shocks, stemming precisely from the technological
        improvements reflected in steadfastly declining market prices. As such, these
        unobservable factors can be adequately controlled for by the time fixed effects in
        the model with homogeneous parameters. By contrast, unobservable shocks to the
        other types of capital seemingly have a different nature. Hence, in this case, we
        expect neglected heterogeneity across countries and sectors to play an important
        role in contributing to overall cross-sectional dependence. Next, we relax the
        assumption of homogeneous parameters across country-sector pairs by implementing
        the Mean Group approach. The results are in Table 3. We first consider variables
        in deviations from their sample mean in the different years, which allows us to
        control for unobservables under the maintained assumption that they have common
        impact on the cross-section units (the corresponding estimates are in the columns
        with CDMG headings). The estimated parameters of interest are highly significant
        throughout. The long run elasticities (in absolute value) are half in size
        compared to the regression with homogeneous parameters. By contrast, the estimates
        of the error correction term point to a much faster speed of adjustment for all
        the assets. The residuals are in general stationary. However, in general, the
        ability to control for strong cross-sectional dependence is not particularly
        satisfactory. Results from the CCE version of the MG estimator are reported in the
        CCEMG columns. Strikingly, the speed of adjustment for computers is much faster
        than the previous estimates would suggest. Looking at the diagnostics shows that
        the residuals from all the equations are stationary, while cross-sectional
        dependence also appears significantly reduced for all asset types, except for
        computers. The combined reading of these regression diagnostics leads us to prefer
        the CCEMG estimates. The estimated long run substitution elasticities, of the same
        order of magnitude as the CDMG estimates but with a lower dispersion, are centered
        on 0.5, a value that does not deviate substantially from the bulk of the results
        in the literature obtained with different techniques and data samples (Chirinko,
        2008). Table 4 reports the p-values of the pairwise Wald statistics testing the
        equality of the long run elasticities in Tables 2 and 3. The test results for the
        homogeneous parameter models suggest the clustering of capital assets into two
        classes. The long run elasticities of the fast depreciating assets are not
        statistically different from one another, although at varying significance levels.
        Likewise, structures and other machinery and equipment display statistically
        similar elasticities. These results are broadly confirmed when the Mean Group
        estimator with demeaned variables is used. However, our preferred MG estimator
        with common correlated effects points to a much lower degree of differentiation of
        the long run elasticities. In particular, the p-values confirm that the hypothesis
        of equality in general cannot be rejected, although only marginally in the
        comparison between computers and the long-lived assets, i.e. structures and other
        machinery and equipment.

<h>CONCLUSIONS</h>
-----------

Empirical models of investment for aggregate capital may be plagued by inherent biases
because of neglected heterogeneity originating from asset and sector specificities. In
this paper, we investigate the effects of imposing homogeneity on the long run
substitution elasticity using a panel of 23 sectors in 10 OECD countries over the period
1984–2007. We perform the analysis for capital stock aggregates as well as for individual
asset types – namely computers, communication equipment, transportation equipment, other
machinery and equipment, and structures. We further relax homogeneity by using panel
techniques with heterogeneous parameters next to the standard pooled models. We find that
the tax-adjusted user cost significantly influences capital accumulation, both for
aggregate and disaggregated series. Results from the standard two-way fixed effects model
suggest that long-lived assets displays statistically similar long run elasticities,
consistent in size with the unit benchmark. We do not find significant differences also
among the elasticities short-lived assets, which are, expectedly, also smaller in
magnitude. However, conventional panel data models, by imposing parameter homogeneity
across countries and sectors, increase the risk of spurious regression and do not correct
for cross-sectional correlation in the residuals. In this respect, the homogeneity
assumption proves critical for virtually all assets, except computers, for which we can
pin down the common supply side nature of technological shocks. Allowing for heterogeneous
parameters reduces both the magnitude and the dispersion of the estimated long run
elasticities for the different assets types. Once we account for unobserved common factors
affecting investment using cross-section averages in the country-industry regressions, we
cannot reject the hypothesis that the long run substitution elasticities are statistically
similar across asset types. Moreover, we concur with the evidence of a more muted impact
than the neoclassical unit benchmark.


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----------

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<ART>China's increasing global influence: Changes in international growth linkages
=============================================================================

Authors: Erdenebat Bataa, Denise R. Osborn, Marianne Sensier
DOI: 10.1016/j.econmod.2018.05.014
Year: 2018  |  Pages: 194-206
ASJC codes: 2002
Keywords: China, Globalisation, International growth, Structural breaks

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Changes in linkages between growth in the USA, Euro area and China are investigated utilising an iterative procedure for detecting structural breaks in VAR coefficients and disturbance covariance matrix. We find dynamics to be unchanged and, accounting for volatility changes, cross-country correlations are constant until the end of 2007. Although largely isolated from the other large economies until 2007, growth in China is subsequently strongly related to that of the US and the Euro area. The effects are illustrated using generalised impulse responses and forecast error variance decompositions. The increased international synchronisation found may be associated with the effects of the Great Recession on the US and Euro area together with China's extraordinary export growth since joining the World Trade Organisation in 2001.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The economic rise of China over the last four decades is well-documented, with its share
of world GDP rising from less than 2% in 1979 to almost 15% in 2016, alongside its share
of world trade in the export of goods increasing from 0.8% in 1979 to 13% in 2016.1
Indeed, China overtook the US in 2007 to become the world's largest exporter of goods.
Although relatively few studies focussed on the role of China in the international economy
until its rise was cemented by overtaking Japan as the world's second largest economy in
2009 (by share of world GDP), it is now attracting a great deal of attention. For example,
recent studies undertaken within the IMF examine the nature and extent of international
spillovers from China, including Arora and Vamvakidis (2011), Blagrave and Vesperoni
(2016) and Furceri et al. (2017). Other authors, including Cesa-Bianchi et al. (2012),
Dreger and Zhang (2014), Osborn and Vehbi (2015) and Pang and Siklos (2016), also examine
how shocks to growth in China affect other economies, while related studies focus on the
role played by China for exchange rates and inflation (for example, Granville et al.,
2011, Metelli and Natoli, 2017). Although much of this work is motivated by the growing
importance of China, empirical analyses nevertheless typically assume constancy over time.
The aim of the present paper is to inform discussion about the nature and timing of any
change(s) in growth relationships across the world's major economic blocks by applying
formal structural break tests to a VAR model for GDP growth in the US, China and the Euro
area. Previous studies that consider time-variation in China's relationship with other
economies include Fidrmuc et al. (2014), Furceri et al. (2017) and Osborn and Vehbi
(2015), but the methods they employ are not designed to pinpoint the nature of change and
when this occurred. However, through a structural breaks analysis, we examine evidence for
change in the cross-country dynamics of growth, its volatility and the strength of
contemporaneous growth linkages. Although methods such as random coefficient models and
rolling regressions can be employed to capture change, we prefer to take a structural
breaks perspective because it does not require a priori assumptions about the existence or
timing of change, and hence may be particularly useful for examining the emergence of
China as an economic force. The implications of the breaks we uncover are explored through
impulse response functions and forecast error variance decompositions. Following Diebold
and Yilmaz (2015), our principal results are not based on any assumed cross-country causal
ordering for growth ‘shocks’, but employ the generalised techniques of Koop et al. (1996)
and Pesaran and Shin (1998). We employ quarterly data over 1975 to 2015, allowing us to
focus on changes in international growth affiliations in the post-Bretton Woods period.
Although there would be some advantages in expanding the analysis beyond the US, the Euro
area and China, difficulties associated with econometric inference for multiple breaks in
a system with a limited amount of data means that parsimony is required in the number of
economies included. We study the Euro area as an aggregate, in order to recognise the
international importance of this economic region, with aggregate output comparable to the
US. Breaks are examined within our three equation system using the iterative testing
procedure of Bataa et al. (2013), which not only separates coefficient and covariance
breaks, but also further decomposes covariance breaks into variance and correlation
breaks. While the broad approach is similar to that employed by Doyle and Faust (2005),
who study changes in linkages between G7 countries, ours is more flexible in that we
neither specify a priori the number of breaks nor are coefficient and covariance breaks
required to be contemporaneous. Further, we separate correlations from volatilities, which
is crucial since the former measure the strength of contemporaneous linkages, whereas
volatility changes may arise from purely domestic factors. Our results imply that breaks
in the contemporaneous correlations of ‘shocks’ are the most important feature of changing
international growth affiliations. More specifically, a correlation break around 2007
evidences the growing importance of China, with substantially increased comovement across
the three economies after this time. On the other hand, no changes in cross-country
dynamic interactions (breaks in the VAR coefficients) are found. Due to the greater
integration of China into the international economy, the effect of a one standard
deviation ‘shock’ to its growth is associated with strong growth effects for both the US
and the Euro area, whereas growth in China was largely isolated from these other economies
until 2007. However, the greater integration of China also has the consequence that its
growth volatility is also now more closely associated with growth shocks from these other
economies. The structure of this paper is as follows. Section 2 discusses data, with
Section 3 then outlining our methodology for measuring linkages; an example of the role of
volatility breaks and an overview of the methodology employed for econometric inference
can be found in the Appendix. Our principal results on growth linkages are presented in
Section 4, while Section 5 provides some discussion and conclusions.

<h>DATA</h>
----

Our analysis employs quarterly real GDP growth rates of the US, Euro area and China over
the period 1975Q2 to 2015Q2. All data are seasonally adjusted and, except for China before
2011, obtained from the OECD database.2 Data for China starts in 2011Q1 in that database,
with growth rates for the earlier period computed using Abeysinghe and Rajaguru's (2004)
estimates of real seasonally adjusted quarterly GDP for China. Abeysinghe and Rajaguru
(2004) interpolate available annual data through the Chow-Lin technique that exploits
information in related quarterly series (namely M1 and total external trade) and observed
autocorrelation, and hence the estimated values are anticipated to be more reliable than
those based on univariate interpolation. We acknowledge that there is widespread doubt
about the quality of historical data relating to the Chinese economy; see, for example,
the study of quarterly GDP by Franses and Mees (2013). Nevertheless, there is little that
individual researchers can do beyond working with the available data and, despite its
limitations, we consider this data to be sufficiently reliable to show the patterns of
growth in the real GDP of China. Of course, the Euro area came into existence only in 1999
and its membership has expanded since that date. To maintain a consistent composition, our
Euro area data relate to the original ‘Euro 12’ (denoted EU12), namely the twelve
countries that comprised the Euro area at the launch of the physical notes and coins in
January 2002.3 EU12 is used in preference to an aggregate for the entire Euro area because
of the changing country composition of the latter. The growth rate in each case is
measured as 100 times the first difference of the log real GDP values. Alongside positive
association between US and EU12 growth rates, the rise of China is evident in Fig. 1, with
its growth rate typically being substantially above than the others since at least the
early 1980s. The Great Recession is clearly visible as a decline in growth for each
country around 2008/2009, albeit with that for China remaining positive. The figure also
indicates that all three economies may have experienced changes in the volatility of
growth over our sample period. Although some changes in patterns may be seen in the
figure, it is nevertheless important to undertake formal analysis in order to confirm (or
otherwise) their nature, since they could be due to random variation rather than changes
in the underlying process. Our analysis employs the quarterly growth rates of Fig. 1.
Although some researchers filter GDP growth rate data in order to remove very short run
fluctuations and hence concentrate on the so-called business cycle frequencies, such
filtering has substantial consequences for the dynamics of the process and hence we prefer
to analyse unfiltered growth rate data.

<h>MEASURING GROWTH LINKAGES</h>
-------------------------

As already explained, our analysis is based on a VAR model for GDP growth in the US, Euro
Area and China. In common with many VAR analyses, we employ the tools of impulse response
functions and forecast error variance decompositions in order to examine the nature of
interactions across variables (in our case, the three economies). However, our analysis is
distinctive in two respects. Firstly, employing the methodology of Bataa et al. (2013), we
examine whether changes have occurred in the parameters of the VAR; details of the
procedure can be found in that paper and is outlined in Appendix 6.2. Sufficient to note
here that, although Doyle and Faust (2005) find evidence of breaks in both the VAR
coefficients and the covariance matrix for international output growth, such breaks need
not occur with the same frequency or at the same dates, as they assume. Previous studies
focusing on the univariate properties of output growth imply volatility declines might be
anticipated in the early 1980s (see, for example, Sensier and van Dijk, 2004), whereas
globalisation may affect dynamic linkages and contemporaneous correlations from the latter
part of the century (Kose et al., 2008). Therefore, our analysis first examines whether
the coefficients, disturbance volatilities and correlations of our VAR change over time.
The second distinctive feature of our analysis is that, when comparing effects over
different sub-periods, we allow shocks across economies to be correlated by utilising the
generalised methodology associated with Koop et al. (1996), Pesaran and Shin (1998),
Diebold and Yilmaz (2015, 2014, 2012), and others. For some VAR analyses, it is plausible
to impose restrictions in order to deliver orthogonalised shocks for each equation.
However, such restrictions can be difficult to justify for cross-country growth spillovers
between the major international economies, and hence we prefer to use generalised
measures. Nevertheless, for comparison purposes, we also provide results for the VAR
orthogonalised using contemporaneous ordering restrictions, in which the US is ordered
first, followed by EU12 and then China. Sections 3.1 and 3.2 describe the linkage measures
employed in our analysis. Once the dates of structural breaks are identified, the measures
discussed in this section become regime-specific, in that they relate to the estimated
model parameter for the specific sub-period of time. When horizons such as one or two
years ahead are considered, the measures computed implicitly assume that no structural
break occurs within the horizon considered. The calculation of confidence intervals,
included in the results of the next section, is discussed in Appendix 6.2.

<hs>  Impulse responses</hs>
  ~~~~~~~~~~~~~~~~~

It is important for the interpretation of both OIRFs and GIRFs to appreciate that these
are influenced by both the disturbance correlations and volatilities of the VAR, that is
by both P and D of (3). Consequently, the VAR coefficients, disturbance (or shock)
standard deviations and correlations all play important roles when measuring the cross-
country effects of a shock to growth. In particular, a break in any of the three
components will, in general, affect both OIRFs and GIRFs. The simple example in the
Appendix provides an illustration of the effects of volatility change in the VAR
disturbances on these measures.

<hs>  Growth volatility effects</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~

In addition to GIRFs, Pesaran and Shin (1998) define the generalised forecast error
variance decomposition (GFEVD). Diebold and Yilmaz (2015, 2014, 2012) build on the GFEVD
concept, applying the results to financial markets and, in Diebold and Yilmaz (2015), to
the international growth context. Their latter papers (Diebold and Yilmaz, 2015, 2014)
refer to GFEVDs as measures of ‘connectedness’, but we prefer to refer to such measures in
our context as growth volatility linkages. In any case, some of our definitions differ
from the corresponding expressions employed by Diebold and Yilmaz (2015, 2014), as
explained below.

<h>RESULTS</h>
-------

We now turn to the principal interest of this paper, namely changes in international
growth linkages and China's increasing role in the world economy. Subsection 4.1 provides
evidence on the structural breaks in the three-economy VAR model of (1) for the US, EU12
and China, while the implications for international growth linkages are discussed in
subsections 4.2 and 4.3.

<hs>  Structural breaks</hs>
  ~~~~~~~~~~~~~~~~~

Structural break testing requires the researcher to set a priori the maximum number of
breaks that can occur in the sample period (M) and the minimum percentage (ɛ) of the
sample within each regime identified between breaks. We specify these as M = 5 and ɛ =
15%, with the aim of having sufficient observations in each detected regime for reliable
inference while also being able to detect important changes during the sample period. It
is important to appreciate, however, that these values apply separately when considering
coefficients and the covariance matrix, since we employ the methodology of Bataa et al.
(2013), outlined in Appendix 6.2. For our sample period, the 15% minimum regime length
requires any initial break to occur after the second quarter of 1981 and any final break
before the third quarter of 2009, with at least 6 years (24 quarters) between two breaks
of the same (coefficient or covariance) form. The maximum of five breaks considered is
fairly arbitrary, but appears reasonable in our sample covering four decades. We employ a
VAR with p = 1, identified using the Hannan-Quinn criterion and all hypothesis tests are
conducted at a 5 percent significance level. Table 1 (panel A) shows an apparent single
break in the VAR coefficients in 2009Q2 by the asymptotic WDMax test of Qu and Perron
(2007), applied in the iterative coefficient/covariance break testing procedure of Bataa
et al. (2013). However, the finite sample bootstrap test of Bataa et al. (2013) finds the
single break identified by the asymptotic procedure to be insignificant, with a p-value
over 50 percent. Thus we conclude there is no statistically significant change in the VAR
coefficients. This initial result is itself notable in the light of the changes in the
international economy over the period that we study, and implies that any changes apply
within the covariance matrix of the shocks rather than the temporal dynamics. The
modelling implication is that all subsequent analysis is based on a VAR with time-
invariant coefficients. Panel A of Table 3 presents the estimated VAR coefficients and
their significance. These indicate statistically significant growth persistence (positive
own lag coefficient) in all three economies. Further, there is evidence of positive
Granger causality in growth from the US to EU12, with the reverse (EU12 to the US)
coefficient also positive and close to significance at the 5 percent level7. The relative
isolation of China from direct dynamic effects originating in the other major economies is
seen in the lagged VAR coefficients relating to China (as either the dependent or
explanatory variable) being both numerically small and statistically insignificant. In
contrast to the constant VAR coefficients, panel B of Table 1 shows three breaks in the
VAR covariance matrix, with estimated dates of 1983Q4, 1993Q3 and 2007Q4, and all are
highly significant according to both the asymptotic (WDMax and sequential) and the
bootstrap tests. Using a sample ending in 2002, Doyle and Faust (2005) identify breaks at
similar dates to ours, namely in 1981Q1 and 1992Q2, in their VAR for GDP growth for the
G-7 countries. However, the methodology available to Doyle and Faust (2005) considers only
coincident breaks across coefficients, variances and correlations, whereas our finding of
unchanged coefficients implies that relevant breaks in our VAR are confined to the
disturbance covariance matrix. The focus of much of our empirical analysis is, therefore,
the nature of changes in the volatilities and cross-country correlations of growth in
these major economies and how such changes impact on spillovers between them. When
considering cross-market relationships, the finance literature has long recognised the
importance of distinguishing between changes in volatility and changes in correlations,
since the former may be due to specific market influences whereas the latter measure the
strength of interlinkages; for example, see Longin and Solnik (1995). The same
considerations apply in our analysis of cross-country growth linkages, and hence it is
important to control for volatility changes so that these do not contaminate an
examination of correlations. Table 2 therefore decomposes changes in the covariance matrix
of our international growth VAR, with volatility considered in panel A and correlations in
panel B. A joint bootstrap test that volatility in the three economies is unchanged at
each covariance break date is rejected at significance levels of 2 percent or less.
Further investigation by considering each country individually indicates that the 1983
volatility break emanates from only the US, which is a manifestation in our data of the
so-called Great Moderation (McConnell and Perez-Quiros, 2000; Sensier and van Dijk, 2004;
Stock and Watson, 2005), whereas the 1993 break is associated with highly significant
volatility reductions for China and the EU12, but the US is unaffected (see the volatility
estimates in Panel B of Table 3,8 which are computed with restrictions imposed based on
the individual volatility test results of panel A of Table 2 using a 5% significance
level). The EU12 volatility reduction around this time has been found in other studies
(see, for example, Perez et al., 2006) and can be associated with the move towards greater
European integration signalled by the Maastricht Treaty bringing lower growth volatility
for the EU12 economy. Interpretation of the volatility decline for China at this date is
more difficult, partly because of the lower reliability of China GDP data, particularly in
the earlier part of the sample. Finally, the significant change in volatility in 2007Q4 is
associated particularly with a substantial increase for EU12, although Table 2 also
indicates some evidence (with a p-value of 7.5%) of a change also for the US. This break
for the Euro area and (possibly) the US may be associated with the onset of the Great
Recession in 2008, with EU12 volatility more than doubling after this break. No break is
detected in China at this time. Employing the standard deviation estimates of Table 3,
panel B of Table 2 investigates the nature of correlation changes at the covariance break
dates. In contrast to the significance of volatility changes at all three dates,
correlations alter (according to 5% significance) only at the end of 2007 and hence we
recognise only two regimes for the matrix P. Indeed, until the end of 2007, the
contemporaneous correlations are small9 and a bootstrap test that the residual
correlations for each economy with the other two are jointly zero is not rejected (panel
B, Table 2). In other words, prior to the end of 2007, none of the three major economies
exhibited statistically significant contemporaneous (within quarter) growth linkages with
the other two and the correlations are consequently imposed at zero in panel C of Table 3.
Thereafter, the zero correlation null hypothesis is clearly rejected; the resulting
correlations of the US with both the EU12 and China are about 0.4, with that between EU12
and China higher at 0.6. The period from the end of 2007 has therefore seen a very
substantial change in international growth linkages, from a situation of effectively no
contemporaneous association to one of strong and positive cross-economy effects. Our
dating of this change is supported by the finding of Fidrmuc et al. (2014) of increased
synchronisation of short-term GDP growth between China and individual G7 countries from
2006. Whereas the US and particularly the Euro area have seen relatively weak growth since
the onset of the Great Recession, the first decade of the 21st century was notable for
China's entry into the World Trade Organisation (December 2001) and the increasing role it
has subsequently played in world trade (see the discussion in Section 5). Bearing in mind
the small dynamic spillovers to and from China revealed by the VAR coefficients, the
period since 2007 is therefore not only one in which China has important interactions with
the other two major economies, but the cross-country effects of growth ‘surprises’ are
seen quickly, namely within a quarter. For reference, Tables 2 and 3 also provide relevant
results for a VAR which ignores covariance breaks. A key consequence of such an analysis
is that China would appear to be contemporaneously uncorrelated with the other major
economies, with the zero correlation test p-value of nearly 12% in panel B of Table 2 for
the no break model. Therefore, in contrast to the strong positive contemporaneous
correlations estimated for the period from 2008 in Table 3 (panel C) when covariance
breaks are recognised, correlations for China with both the US and EU12 are imposed at
zero in the no breaks model. Further, the US-EU12 correlations in the no breaks model are
moderate at 0.24. To the extent that our results from 2008 reflect on-going cross-country
growth linkages, use of a constant parameter VAR analysis would be seriously misleading.

<hs>  Impulse responses</hs>
  ~~~~~~~~~~~~~~~~~

As noted in Section 3, impulse responses change with any break in the parameters of a VAR
model. Based on the identified breaks of subsection 4.1, Figs. 2–4 show growth cumulated
GIRFs and OIRFs for a one standard deviation shock applied to each of the three economies.
Since the disturbance covariance matrices are diagonal for all sub-periods until 2007Q4
(Table 3), GIRFs and OIRFs coincide until that date. With VAR coefficients constant over
time, the estimated impulse responses in each of Figs. 2–4 until 2007Q4 differ only due to
the magnitude of the one standard deviation shock applied. Reflecting these size effects,
note that the vertical scale sometimes changes. The volatility results in Table 2 imply a
single regime from 1984 to 2007 (the period of the Great Moderation) for US shocks, and
over 1975Q3 to 1993Q3 for each of EU12 and China shocks. These volatility restrictions are
imposed in the results presented, with the sub-periods identified in the headings of the
figures reflecting the volatility regimes relevant to the economy of the originating
shock. For example, in Fig. 2, a US shock is of magnitude 1.16 percent in the sub-period
to 1983Q4, but declines to 0.54 from 1984Q1 onwards. Although no volatility break is
detected (using 5% significance) for the US at the Great Recession (2007Q4), the
correlation break at this date (see Tables 2 and 3) leads to a new sub-period applying for
impulse responses resulting from a US shock. The OIRFs we consider impose a
contemporaneous causal ordering of the US, followed by EU12 and then China. Therefore, the
GIRFs and OIRFs are identical for the US (the first variable in the ordered VAR) also in
the final sub-period and are consequently not shown separately in Fig. 2. For each graph,
one and two standard error confidence intervals are included around the estimated
responses, with these obtained as discussed in the Appendix subsection 6.2. For reference,
each graph also includes corresponding information obtained from a VAR in which constant
parameters are assumed (the no breaks model), with that estimated response shown as a blue
dotted line and the corresponding confidence intervals by blue shading. Consider, first,
GIRFs for US shocks in Fig. 2. As already noted, the magnitudes of the shocks differ over
the 1975–1983 and 1984–2007 regimes. Although our model does not find a change in the
magnitude of the US shock in 2007Q4 or a change in the VAR coefficients, the width of the
confidence intervals for the own US responses substantially increase, due to
contemporaneous international linkages now associated with the US. It is also notable that
although the point estimates of these own responses from a model with no breaks are
reasonably close to those for the 2008Q1-2015Q2 sub-period, the no breaks model implies
much tighter confidence intervals. In other words, the no breaks model fails to capture
the uncertainty of the most recent period for the US. Responses by the EU12 and China to
US shocks, also, of course, shift with the Great Moderation due to the relative sizes of
US shocks. Notice also that in both the period before the Great Moderation and since
2007Q4, a one standard deviation US shock leads to a GIRF point estimate for the EU12
growth response of approximately 0.6 percent after about a year. For China, the point
estimate response to a US shock is positive only from 2008, from when it is also
significant according to the one standard error band. Since the size of the US shock does
not change in the latest period, it is now more “potent” due to contemporaneous
international linkages. Although the changed role played by China in the world economy is
illustrated by it responding to US shocks only from 2008, the GIRFs show US shocks to have
positive, and typically highly significant, effects on EU12 growth over the entire sample
period. Historical interactions between growth in the US and the Euro area are emphasized
by Fig. 3, which shows EU12 shocks to have effects on the US which are significant
according to the one standard error bands. Of course, the 1993 volatility reduction for
EU12 leads to responses declining in magnitude and the confidence intervals narrowing. The
figure includes, for the most recent period, both GIRFs and OIRFs. According to the
former, effects of EU12 on the US are largest in the most recent sub-period, due to both
increased EU12 volatility and increased US/EU12 correlation (Table 3). However, use of the
orthogonalised VAR in the final column diminishes the EU12 role for the US since 2008
relative to the use of GIRFs due to the causality assumed. Except for the period between
1993 and 2007 when growth volatility in EU12 was relatively low, the GIRF point estimates
of the own effects of EU12 shocks are relatively constant over time, albeit with wider
confidence bands in the post-2007 period. Until the end of 2007, these shocks have
inconsequential effects on China, but the substantial correlation of the most recent
period leads to positive and significant (according to the one standard error bands)
responses after that date, whether measured by GIRFs or OIRFs. Of particular interest for
our analysis, Fig. 4 presents impulse responses for China shocks. Throughout the period to
2007, the linkages of China shocks with the other two economies are small in magnitude
(indeed, negative for EU12) and not significant according to the one standard error bands;
with a diagonal covariance matrix, these effects come only through the VAR coefficients
(Panel A of Table 3). With increased contemporaneous correlations from 2008, the GIRFs
show strong responses of both other economies to China shocks, with those for EU12 being
significant at two standard errors for short lags. With China ordered last in the
orthogonalised VAR, the OIRFs in Fig. 4 contrast with the GIRFs for the international
spillovers from China shocks for 2008 onwards. In particular, with no contemporaneous
effects allowed to flow from China to these other economies, OIRFs show effectively no
spillovers from growth in China. We consider such a finding to be implausible and hence
concentrate on GIRFs. Therefore, one key result from the GIRFs of Fig. 4 is that China
shocks are important for growth in both the US and the Euro area since 2008. This result
is driven by the strong positive correlations between the China disturbances and those of
the US and EU12 over this period (Panel C of Table 3). Although impulse responses are
shown for a model which does not recognise structural breaks, it should be noted that this
model has zero correlations for China shocks with those of the US and EU12 and hence the
GIRFs for this model find effectively no responses of the other economies to China shocks.
This again emphasizes the importance of recognising the possibility of changes in
international relationships over our sample period, with breaks in the contemporary
correlations of growth shocks being particularly important.

<hs>  Growth volatility</hs>
  ~~~~~~~~~~~~~~~~~

Turning to growth volatility resulting from cross-country shocks, Table 4 provides
forecast error variance decompositions in the form of both GFEVDs and (post-2007) OFEVDs.
Results for horizons h = 1 and h = 4 are shown, with longer horizons being similar to the
latter. The results indicate that, as measured through the GFEVD, growth volatility in all
three economies and across all covariance regimes is primarily associated with own shocks.
This applies especially for China, where at least 99% of the growth forecast error
variance at both horizons considered is associated with own shocks. Although a little
lower, the corresponding figures are 90% or more for the US. The lowest percentage applies
in EU12, where own shocks are associated with around 85% of volatility at a one year
horizon over 1975–1983 and during the European integration phase of 1994–2007. As
discussed in subsection 3.2, the use of GFEVDs implies that decompositions do not sum to
100% across shocks unless the covariance matrix is diagonal, which is the case in our
model until the end of 2007. However, the positive correlations from 2008 mean that the
sums of GFEVDs across shocks for each of the three economies substantially exceed this
value in the final sub-period. Although 1983Q4 represents a pure volatility break
according to our test results of Table 2, the results in Table 4 indicate that this brings
about a marked change in US/EU12 volatility linkages. In particular, whereas US shocks are
associated with about 15% of EU12 growth forecast error volatility at h = 4 in the earlier
sub-period, the decline in US volatility during the Great Moderation causes this to drop
to only 3% over the decade from 1984, before subsequently increasing again. Until 2008,
however, volatility in China is effectively isolated from these other major economies. Not
surprisingly in the light of the international shock correlations after 2007, GFEVDs show
shocks in each of the other countries to be important (and generally statistically
significant) for growth volatility in all three economies in the final sub-period. On the
other hand, the use of OFEVDs leads to weaker effects to China from both the EU12 and its
own shocks in this recent period. The final column block, labelled From Others, shows the
total volatility not associated with own innovations, as defined by (7). As discussed in
section 3.2, the GFEVD measure we present here excludes all effects associated with own
shocks. In 1975–1983 and 1994–2007, the converse of the lower volatility percentage
accounted for by own shocks in EU12 is that international growth volatility linkages to
this economy from others are larger (and often more statistically significant) than for
other economies and other sub-periods. However, the strong post-2007 shock correlations
lead to values that are relatively small for all three economies in this period, and these
are all less than one standard error in magnitude. Bidirectional comparisons obtained
using (6) are also shown in Table 4. The GFEVD results indicate that net volatility
linkages from the US to EU12 are positive until the end of 2007, with the exception of the
sub-period following the Great Moderation (1984–1993). Over the remaining two sub-periods
US shocks are estimated to account for substantially more EU12 forecast error volatility
than the EU12 does for the US, underlining the international role played by the US.
Although negative, the net US-EU12 GFEVD values are very small post-2007, again reflecting
the strong shock correlation during this time. Perhaps surprisingly, the GFEVD estimates
indicate that the US has a negative net growth volatility linkage to China (that is, the
net value is in the direction of China to the US) over all sub-periods, but the values are
relatively small and typically less than one standard error in magnitude. This last
comment applies also when net GFEVD volatility spillovers between EU12 and China are
considered. Orthogonalisation increases net growth volatility linkages post-2008. Of
course, if a constant parameter model is employed, the changes over time discussed above
that arise as a result of both volatility and correlation breaks cannot be detected.
Nevertheless, the general patterns can be seen of international effects on growth
volatility being most marked for EU12, with positive net volatility bilateral linkages
from the US to EU12, but net linkages with China being small. An interesting comparison
between the two (generalised versus orthogonalised) FEVD approaches is provided by the
average of the percentage volatility from others, as defined in (8) and shown in the
bottom horizontal block of Table 4. The averages obtained from the GFEVD are relatively
small (6% or less) and have not increased in the recent period, suggesting that
international growth volatility linkages have remained rather muted throughout our sample
period. In contrast, causal ordering due to orthogonalisation suggests a huge increase in
growth volatility due to shocks originating in other economies in the period after 2007Q4,
being over 20% for EU12 and around 40% for China. Once again, however, we consider these
orthogonalised results to be a consequence of the imposition of ordering restrictions that
do not reflect current macroeconomic relationships. Indeed, increased contemporaneous
correlation but low net growth volatility linkages (as indicated by FEVDs post-2007) are
consistent with increased synchronisation of growth across these major economies.

<h>DISCUSSION AND CONCLUSIONS</h>
--------------------------

Although it is beyond the scope of the present paper to analyse in detail the reasons why
China has become such a force in the world economy, some comments are nevertheless in
order. Many recent studies, including Autor et al. (2016), Caporale et al. (2015) and Yao
(2014), point to China's remarkable growth since the 1970s being led by exports. After
increasing quickly from then until 2008, Yao (2014) also notes that China's share of world
exports has subsequently been in line with its share of world GDP, which is compatible
with our finding of a new regime of China's integration in the world economy from 2008.
Caporale et al. (2015) study the changing composition of China's trade, documenting a
shift from labour-intensive to capital- and technology-intensive exports over two decades
to 2012; see also Autor et al. (2016). The key to China's increased trade in the current
century is its accession to the World Trade Organisation at the end of 2001 (Autor et al.,
2016; Yao, 2014). In particular, China's exports of goods rose dramatically after it
joined the WTO, and (as noted in the Introduction) it's share overtook the US in 2007.
This suggests our finding of greater integration for China with the US and Euro area from
2008 is associated with its role as a major trading nation. Empirical work of the type
undertaken here might be extended to other countries, to examine whether the changed
affiliations of China with the US and Euro area apply more generally and with similar
dates of change. Based on our findings, such analyses might place particular focus on the
role of trade and China's accession to the WTO. The results of this study are in line with
these analyses and emphasise the key role played by China in the world economy over the
last decade or so. Using a VAR model to capture GDP growth interactions across the US,
Euro area and China, our principal finding is the substantial increase in the
contemporaneous correlations of cross-country disturbances at the end of 2007. Using
wavelet analysis, Fidrmuc et al. (2014) also detect increased synchronisation of GDP
growth in China with major economies from around this date. Since China's growth was
effectively isolated from influences from these other major economies until 2007, this
most recent sub-period is very different from earlier ones in terms of the synchronicity
of international growth. Consequently, cross-country shock responses to and from China are
not only more marked, but these occur more quickly then previously, with the China-Euro
area growth relationship being particularly strong. Volatility linkages have also become
important since 2008, with China's volatility more strongly associated with growth shocks
in the other economies. Interestingly, however, net growth volatility linkages in this
period are in the direction of China to the US, underlining its increased role for even
the largest economy in the world.


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<ART>Climatic conditions and child height: Sex-specific vulnerability and the protective effects of sanitation and food markets in Nepal
================================================================================

Authors: Prajula Mulmi, Steven A. Block, Gerald E. Shively, William A. Masters
DOI: 10.1016/j.ehb.2016.07.002
Year: 2016  |  Pages: 63-75
ASJC codes: 2001
Keywords: Child health, Child nutrition, Maternal health, Sanitation, Seasonality

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Environmental conditions in early life are known to have impacts on later health outcomes, but causal mechanisms and potential remedies have been difficult to discern. This paper uses the Nepal Demographic and Health Surveys of 2006 and 2011, combined with earlier NASA satellite observations of variation in the Normalized Difference Vegetation Index (NDVI) at each child's location and time of birth to identify the trimesters of gestation and periods of infancy when climate variation is linked to attained height later in life. We find significant differences by sex: males are most affected by conditions in their second trimester of gestation, and females in the first three months after birth. Each 100-point difference in NDVI at those times is associated with a difference in height-for-age z-score (HAZ) measured at age 12–59 months of 0.088 for boys and 0.054 for girls, an effect size similar to that of moving within the distribution of household wealth by close to one quintile for boys and one decile for girls. The entire seasonal change in NDVI from peak to trough is approximately 200–300 points during the 2000–2011 study period, implying a seasonal effect on HAZ similar to one to three quintiles of household wealth. This effect is observed only in households without toilets; in households with toilets, there is no seasonal fluctuation, implying protection against climatic conditions that facilitate disease transmission. We also use data from the Nepal Living Standards Surveys on district-level agricultural production and marketing, and find a climate effect on child growth only in districts where households’ food consumption derives primarily from their own production. Robustness tests find no evidence of selection effects, and placebo regression results reveal no significant artefactual correlations. The timing and sex-specificity of climatic effects are consistent with previous studies, while the protective effects of household sanitation and food markets are novel indications of mechanisms by which households can gain resilience against adverse climatic conditions.

--------------------------------------------------------------------------------


<h>INTRODUCTION AND MOTIVATION</h>
---------------------------

Attained height is among the most important indicators of childhood health or deprivation.
Approximately 25 percent of each year’s worldwide cohort of infants grow up to be stunted,
and the dietary or disease conditions that limit linear growth in childhood also
contribute to poor educational attainment, low earnings, and high mortality rates later in
life (IFPRI, 2014; UNICEF, 2015). Stunting rates have been especially high in Nepal, where
extreme poverty and political instability led to rates as high as 57 percent in 2001,
before declining to 41 percent in 2011 (United Nations, 2013). Despite this improvement,
Nepal remains one of the 10 countries in the world with the highest stunting prevalence
(UNICEF, 2014), making it a high-priority location for research into increasingly
effective ways of protecting children from harmful early-life circumstances. Socioeconomic
factors associated with stunting in Nepal are described by Headey and Hoddinott (2015),
who show how changes in household and community-level characteristics help explain local
variation and the overall improvement in this indicator from 2001 to 2011. Key changes
involved both greater household sanitation and access to improved diets, which are pillars
of the Nepal government’s multisector nutrition plan (Nepal NPC, 2012). Despite this
progress, however, poor sanitation and inadequate food intake remain widespread and are
likely to be worsened by rising temperatures and more variable rainfall associated with
climate change (IPCC, 2014). This paper uses satellite data on vegetation near each
child’s home as an indicator of changing agroclimatic conditions, with randomness in the
month of birth providing a natural experiment in the timing of exposure to more or less
advantageous circumstances. Our use of variation in birth timing relative to changes in
climatic conditions contribute to a rapidly growing body of literature using natural
experiments to study the determinants of human health (Angrist and Krueger, 2001; Akresh
et al., 2011; Lokshin and Radyakin, 2012; Tiwari et al., 2013; Brown et al., 2014),
addressing the timing and mechanisms by which early conditions influence later outcomes
(Skoufias and Vinha, 2012; Kumar et al., 2016 ; Schultz-Nielsen et al., 2016). Our
identification strategy takes a difference-in-differences approach, testing whether
household sanitation and district-level food markets can protect children against the
health consequences of unfavorable agroclimatic conditions at sensitive times in their
early growth and development. The specific data we use are the Nepal Demographic Health
Survey (NDHS) for child health, sanitation, and other household characteristics from 2006
and 2011, combined with Normalized Difference Vegetation Index (NDVI) data from the
National Aeronautics and Space Administration (NASA) for 2000–2012 at each child’s
location, and the Nepal Living Standard Survey (NLSS) to characterize local agricultural
markets for 2003–2004 and 2010–2011. By combining three kinds of data, we are able to
identify patterns in attained heights of children observed at 12–59 months of age, and
test whether sanitation and food markets limited their association with agroclimatic
conditions experienced during gestation and the first year after birth. We find the
underlying patterns to be sex-specific, with systematic differences in how later heights
relate to NDVI fluctuations that occurred during infancy and pregnancy. These differences
are consistent with both gender bias in infant care (Maccini and Yang, 2009) and
physiological differences in fetal development before the sex of the child is known
(DiPietro and Voegtline, 2015; Rosenfeld, 2015). We find that improved household
sanitation and more commercialized food markets limit both kinds of vulnerability,
providing significant protection from agroclimatic conditions for both pregnant mothers
and infants.

<hs>  Agriculture and climate in Nepal</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Nepal is a landlocked country with a population of approximately 27 million people, of
whom about 85 percent live in rural areas (Nepal MoHP, 2012) and are highly reliant on
rain-fed agriculture (Nepal MoAD, 2013). The country features three distinct ecological
zones: Mountains (52,000 km2), Hills (61,000 km2), and Terai or lowlands (34,000 km2),
with varying population densities. The Mountain zone has a dry alpine climate and is
situated at the highest altitude (>2500 m), with steep and rugged terrain and short
growing seasons. The Hills have a mostly temperate climate (500–2500 m), and the Terai
(<500 m) has a mostly subtropical and humid climate (Nepal MoHP 2012). Although the Terai
occupies 23 percent of the country’s landmass, it hosts almost half of the population (48
percent) and most of the cultivable land (56 percent) (Nepal MoAD, 2013). The most
commonly grown crops are cereals including maize, millet, barley, rice, and wheat (WFP,
2014). Consistent with global trends of increasing temperature and erratic rainfall
patterns (NASA, 2015), temperatures in Nepal increased by 1.5 °C over the period from 1978
to 2005 (Krishnamurthy et al., 2013), while rainfall declined in frequency and increased
in intensity (Malla, 2008). The impacts of climate trends and fluctuations can be seen
through changes in sowing dates, crop duration, crop yields, and management practices
(IPCC, 2014). Between 1978 and 2008, the summer months (May–August) became increasingly
hot and wet, and winter months (November–February) became colder and drier. During that
time, the higher levels of rainfall in summer increased rice yields but decreased yields
for other crops, while lower levels of rainfall in winter decreased maize yields (Joshi et
al., 2011). For this paper, we use NDVI data to summarize the complex pattern of variation
in both rainfall and temperature, providing a simple index of changing agroecological
conditions in the area around each child’s home.

<hs>  Seasonality and child nutrition</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Seasonal variation and other climatic changes have a clear link to the nutritional status
of children in many contexts, even in industrialized countries (Chodick et al., 2009). In
the UK, for example, babies born in winter have significantly lower birth weights,
educational attainment, and adult heights, perhaps as a result of low vitamin D levels
during early life (Day et al., 2015). In the United States, children conceived in the
summer have a higher prevalence of birth defects (McKinnish et al., 2014) and different
genetic characteristics (Rietveld and Webbink, 2016). Some seasonal patterns may be the
result of selection effects, as Buckles and Hungerman (2013) show in their study of winter
births in the United States which occur disproportionately among disadvantaged youths.
However, in developing countries, studies have repeatedly found relatively large
agroclimatic patterns that cannot be explained by selection effects. For example, in the
Democratic Republic of Congo, Darrouzet-Nardi (2015) shows that children born during wet
seasons grow up to be shorter, with no evidence for selection effects of adverse birth
timing of children with lower levels of household wealth or education. Agroclimatic
fluctuations may affect child nutrition through both disease risk and dietary intake. A
principal source of variation in both kinds of risk is rainfall: children born during
monsoon months in India have lower height and weight than children born during the
fall–winter months (Lokshin and Radyakin, 2012). In addition, rainfall fluctuations in
Indonesia have been shown to affect child health in both rural and urban areas (Yamauchi
2012; Cornwell and Inder, 2015). These associations often depend on the timing of
exposure. For example, Tiwari et al. (2013) show that in Nepal, a child’s weight for age
is positively correlated with rainfall in the previous monsoon season, but negatively
correlated with rainfall in the current monsoon. Temperature may play an independent role,
as suggested by Hu and Li (2016), among others, although Nepal’s complex topography
complicates efforts to analyze the effects of spatial variation in temperature. In any
case, covariance among climatic variables, agricultural conditions, and dietary intake
makes it difficult to distinguish one factor from another. In Malawi, for example, the
prevalence of underweight among children under age five rises during the rainy season,
which is also the preharvest period, when maize prices are highest (Sassi, 2015).

<hs>  Vulnerability in utero and after birth</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Gestation and the first two years after birth are the most critical periods for child
development, and have clear impacts on physical, cognitive, and other outcomes later in
life (Almond, 2006; Black et al., 2013; Hoddinott et al., 2013). Adverse conditions in
utero and during the first two years of life can cause high perinatal mortality and
subsequent stunting (Coffey, 2015) as well as low weight and anemia (Kumar et al., 2016),
low economic productivity (Paxson and Schady, 2007; Hoddinott et al., 2013), and less
academic success (Schultz-Nielsen et al., 2016). Affected children may also have higher
odds of developing cardiovascular disease and other conditions (Popkin et al., 1996;
Sawaya et al., 2003), as set forth in the fetal origins hypothesis of Barker (1995). This
paper expands on the previous literature by using quarterly variation in NDVI to identify
sex-specific differences in the timing of vulnerability before and after birth, and to
test for the possible protective effects of improved sanitation and food markets. Our
focus on sex differences follows that of Skoufias and Vinha (2012), and our attention to
the exact timing of exposure follows Andalon et al. (2014) and Carlson (2015), among
others, building on previous work in South Asia using Demographic and Health Surveys (DHS)
in both India and Nepal that suggest a stronger link between rainfall variation and child
height during early months in infancy than during other periods of a child’s life (Lokshin
and Radyakin, 2012; Tiwari et al., 2013). Moreover, focusing on the growing seasons in
Nepal, other researchers find that anomalies in vegetation density show higher
correlations with stunting during the in utero and infancy phases than in other phases of
a child’s development (Shively et al., 2015). The timing and magnitude of vulnerability to
agroclimatic conditions could differ by the child’s sex. There is a growing body of
evidence suggesting differential effects of prenatal stress on male and female fetuses on
perinatal outcomes (Aibar et al., 2012; Mulla et al., 2013; Persson and Fadl, 2014) and
adult health (Scholte et al., 2015). In general, female fetuses are more resilient and
adaptive to stress than are male fetuses (DiPietro and Voegtline, 2015; Rosenfeld, 2015).
Evidence from studies that examined the effects of stressors such as intrauterine lead and
pesticide exposure, and maternal alcohol and drug use, suggest that exposed male fetuses
are more likely to be born preterm and have poorer scores on developmental assessments
than females (Rosenfeld, 2015). Historical data from Danish cemeteries suggest that males’
heights increased during the 19th century while females’ did not (Jørkov, 2015). In
malnourished populations today, on average boys are more likely to be stunted than girls,
but after birth, when the child’s sex is known, gender discrimination may play an
important role in health outcomes. For example, Maccini and Yang (2009) show that
Indonesian families commonly protected boys more than girls from early-life shocks, and
countries with more gender discrimination in favor of boys have lower rates of stunting in
males relative to females (World Bank, 2008) with intergenerational effects (Osmani and
Sen, 2003).

<hs>  Protective effects of sanitation and food markets</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Numerous interventions could provide protection against the disease transmission and
dietary inadequacy associated with agroclimatic conditions. In this paper, we study two
kinds of variables that are of particular interest to policymakers: household sanitation
and local food markets. Sanitation has become an increasingly important policy tool in
recent years, especially for South Asia (Hammer and Spears, 2016), while the impact of
agricultural commercialization on nutrition has been of longstanding concern around the
world (Von Braun and Kennedy, 1994). The potential efficacy of household sanitation
against stunting operates through preventing fecal–oral transmission of diseases such as
diarrhea and enteropathy, which cause both mortality and stunting through loss of
nutrients, decreased absorption of nutrients, and a weakened immune system (Checkley et
al., 2008; Humphrey 2009). There may also be selection effects, as households with toilets
may have other favorable conditions for child development, but the prevention of disease
transmission provides a clear causal mechanism to explain how sanitation might improve
nutritional status (Coffey and Geruso, 2015) and linear growth (Checkley et al., 2004; Lin
et al., 2013). In this study, we focus on the average effects on each child of having a
toilet in their own household; future work could address the externalities among
households described by Hammer and Spears (2016). The potential efficacy of food markets
is likely to operate primarily through dietary intake, as shown for Ethiopia by Abay and
Hirvonen (2016). As shown by Puentes et al. (2016), total intake, especially of nutrient-
rich foods, can have a major impact on child growth. In this study, we focus on whether
households have access to food from elsewhere than their own farm production, by using
their district’s share of total food consumption that is either purchased or received in-
kind, as opposed to consumed on-farm. We employ district fixed effects to control for
other time-invariant district characteristics, thereby isolating the specific effect of
being in districts where households are more reliant on local conditions and unable to use
markets to improve dietary quality, as in the study by Sibhatu et al. (2015).

<hs>  Identification strategy and data sources</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our study uses a two-stage difference-in-differences design, comparing the association
between child height and earlier agroclimatic conditions among children with different
birth exposure, in households with and without toilets, and in districts with low and high
food market use. The first set of differences exploits a natural experiment in exposure to
different levels of NDVI at each stage of early development, while the second splits the
sample into two groups to isolate the protective effects of sanitation and food markets.
This strategy relies on combining three distinct kinds of information: NDHS data on child
height and household characteristics, NDVI data on agroclimatic conditions, and NLSS data
on agricultural commercialization. With these datasets, we are able to address a number of
potential threats to identification: first, showing that the month of conception is
uncorrelated with maternal and household socioeconomic status or other characteristics;
second, using fixed effects and statistical controls to narrow the parallel-trends
assumption implicit in our method; and third, performing a set of placebo regressions to
demonstrate that results are not an artifact of the method. In all regressions, we control
for observables known to correlate with maternal health and child size, such as parental
education, maternal body mass index (BMI), household wealth, and altitude (Wehby et al.,
2010). The NDHS is a comprehensive, nationally representative survey typically conducted
every five years to gather data on population and health. The NDHS is carried out under
the Ministry of Health and Population and conducted by New ERA as part of the worldwide
DHS program. The DHS uses standardized questionnaires and fieldwork to allow comparisons
across years in demographics and health and nutrition–related variables. This paper uses
two recent rounds of the NDHS conducted in 2006 (February–August) and 2011
(February–June). Both survey rounds use two-stage, stratified sampling, including
households in all 75 districts across all ecological zones and development regions. The
2006 survey uses the 2001 population census for a sampling frame, while the 2011 survey
uses an updated 2001 population census for a sampling frame that accounts for population
growth and internal and external migration. Anthropometrics for children under five years
of age were collected from 5237 and 2335 children in 2006 and 2011, respectively (Nepal
MoHP, 2007, 2012). The NDVI is a measure of vegetation density resulting from the
interaction among rainfall, temperature, and soil fertility over time. Green vegetation,
owing to the presence of chlorophyll, absorbs red (visible) light and reflects near
infrared light, while sparse vegetation reflects more red light and less near infrared
light. NDVI values are measured as NDVI = NIR − RED/NIR + RED. Here, the numerator denotes
the normalized difference between red and near infrared light bands, and the denominator
is the sum of red and near infrared light bands (Weier and Herring, 2000). Those data are
obtained from NASA satellite remote sensors using a Moderate Resolution Imaging
Spectroradiometer (MODIS) Climate Modeling Grid (CMG), which provides data at 5 km
resolution (Shively et al., 2015). The dataset includes monthly NDVI values for 12 years
(February 2000–May 2012) for each child’s location of birth, corresponding with 260 and
289 clusters in 2006 and 2011 NDHS, respectively (Nepal MoHP, 2007, 2012). The full
distributions of NDVI levels for each month are shown in Appendix A. This variable
provides an attractive measure of green biomass and leaf area (Thenkabail et al., 2009),
which in turn depend on available moisture, temperature, and soil fertility as well as
human intervention in response to those underlying conditions (Laidler et al., 2008). NDVI
is also influenced by factors other than plant growth, such as cloud cover and ground
conditions. Although NDVI is not a simple index of climatic conditions or crop production
(Shively et al., 2015), it does provide a powerful measure of trends and fluctuations in
various agroclimatic conditions that could affect child development. The NLSS is a
comprehensive national, multitopic household survey conducted by the Nepal Central Bureau
of Statistics (CBS), using survey methods developed and promoted by the World Bank. The
NLSS uses multistage and stratified sampling with the Population Census 2001 of Nepal as a
sample frame basis. Data collection spans an entire year, unlike the NDHS, in order to
capture the effects of seasonality. The purpose of the NLSS is to assess changes in the
population’s living standards using a combination of panel data and cross-sectional data
for a given survey round. A wide range of topics covered by the NLSS includes poverty and
access to finances, health, education, agriculture and rural development, and labor
markets (Nepal CBS, 2004, 2011). This paper, however, uses only agriculture and rural
development data, which include a range of information on food consumption, food
production, and related expenses. In order to align the time frames between NLSS and NDHS
data, the NLSS II 2003–2004 is merged with the NDHS 2006, and the NLSS III 2010–2011 is
merged with the NDHS 2011 (Shively et al., 2015).

<h>DATA AND RESULTS</h>
----------------

Our main outcome variable is each child’s height-for-age z score (HAZ), defined as the gap
between that child’s measured height and the median height of a healthy population at each
age and sex, expressed in terms of standard deviations (SDs) of the healthy population
(WHO and UNICEF, 2009). Children are classified as stunted when their HAZ is two or more
SDs below the median, but here we focus on HAZ scores as a continuous variable to capture
variation at every level of attained height. In addition, although the NDHS enumerators
measured the length or height of all children under five years of age, here we focus on
heights attained between the child’s first and fifth birthdays, as a function of
agroclimatic conditions experienced both in utero and during the child’s first year after
birth. Control variables include the child’s age in months at the time of measurement,
total number of siblings ever born, maternal age, maternal education and BMI, household
wealth, altitude and region, urban residence, and survey round.

<hs>  Descriptive statistics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

Table 1 shows means and SDs for nutritional outcomes and control variables in addition to
other variables of interest. All data are from the NDHS 2006 and 2011, except for
district-level data on food market participation and distance to market centers, which are
obtained from the two waves of the NLSS. Because later regressions will be performed on
data split by the sex of the child, we show the pooled dataset of all children aged 12–59
months (N = 6127), and the subsamples of boys (n = 3129) and girls (n = 2998). The summary
statistics in Table 1 show that the two subsamples are balanced in all regards, except
that the male subsample is larger and the females have more siblings, which is consistent
with sex-selective stopping rules by which parents seek additional children until they
reach their desired number of boys (Bongaarts, 2013). Turning to agroclimatic conditions,
the NDVI levels to which each child is exposed at each stage of development depends on the
month and location of birth. Fig. 1 shows the seasonal patterns of NDVI variation in
Nepal’s three main regions. Vegetative cover generally peaks during August–October, with
greater month-to-month variation occurring in the Terai region. There is greater
uncertainty in calculating each month’s mean NDVI for the Mountain region, partly because
of smaller sample size: only 87 of the 547 cluster locations for our two NDHS surveys were
in the Mountains, while the rest were almost equally distributed between Hills and Terai.

<hs>  Exploratory regressions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

Our identification strategy relies on randomness in birth timing relative to variation in
agroclimatic conditions around the home. Before proceeding, we test for possible selection
effects, asking whether some kinds of mothers are more likely to conceive in certain
months of the year. Seasonal patterns of conception could result from seasonal migration
of family members, variation in natural fertility, or even deliberate pursuit of
conception at more favorable times. Table 2 tests for selection patterns in a very general
way, using a multinomial logit model of selection for each month of conception, nine
months before the observed month of birth. The results of Table 2 show 12 of 121
coefficients with statistical significance at the 5 percent level or higher. Half of these
are the significant coefficients on altitude between February and August. During that
period, families at higher altitudes are more likely to conceive a child than families at
lower altitudes. Lower altitude places are relatively hot in the summer, so this result is
consistent with Levitas et al. (2013) who found sperm counts and motility to be lower at
warmer times and places. The remaining six coefficients which are significant at the 95
percent level have no clear pattern, confirming the absence of selection effects on the
timing of conception in this context. These results contrast with the strong selection
effects in the United States (Buckles and Hungerman, 2013) but are consistent with studies
elsewhere, such as Taiwan (Fan et al., 2014), India (Lokshin and Radyakin, 2012), and
Nepal itself (Panter-Brick, 1996). Without selection by education or other parental
characteristics for specific birth months, differences in attained height by month of
birth are most likely the result of environmental exposure effects. To identify this
purely seasonal pattern in how birth timing relates to attained heights, we employ
ordinary least squares (OLS) regressions using the following base specification:Yi = β0 +
β1m birthmonthim + δiZi + ui,where Yi indicates the HAZ score of a child aged 12–59
months, birthmonthim is a vector of dummy variables equal to 1 when m = the birth month of
that child and zero otherwise, and Zi is a vector of control variables at the child-,
maternal-, household-, and district levels. District fixed effects are also included, and
standard errors are clustered by birth year and district. To account for the effects of a
child’s age on measured HAZ, as in Cummins (2015), we use two different specifications:
age and age squared in columns 1, 3, and 5, and a linear year of birth term in columns 2,
4, and 6. The two types of age control yield a similar month of birth effects, so for the
remaining tests, we use only the simple age in months and months-squared specification,
and focus attention on the differences between boys and girls in regard to what birth
timing might be relatively unfavorable. Results in Table 3 reveal that the worst month for
all children to be born is April, but boys are also disadvantaged by being born in June
and September relative to the omitted month, January. As shown in Fig. 3 .1, April is one
of the lowest-NDVI months, while September the highest. A few other months have some
correlation with attained heights, and the magnitude of these seasonality effects are very
large: for all children, being born in April has an effect size similar to 1.9 quintiles
of wealth, and for boys, being born in September has an effect size similar to 2.4
quintiles of wealth.

<hs>  Empirical methods</hs>
  ~~~~~~~~~~~~~~~~~

To investigate causal mechanisms and potential remedies for the effect of birth timing on
attained height, we turn to variation in NDVI at each stage of child development during
pregnancy and the first four three-month periods after birth. Our focus is on
heterogeneity and effect modifiers, so we divide the sample into boys and girls to
identify sex-specific vulnerability at each stage of early child development, and then
test for the protective effects of sanitation and food markets by dividing the sample into
households with or without toilets and districts with above- or below-median reliance on
local production as opposed to food purchases or gifts. This split-sample approach, made
possible by our large number of observations, permits variation among subsamples in all
coefficients while avoiding a proliferation of collinear interaction terms. In this
design, exposure to climate variation is a natural experiment to which children are
exposed under conditions that might or might not be protective. Testing for heterogeneity
in treatment response can help identify causal mechanisms, target services to those most
at risk, and help spread desirable effect modifiers. In this case, we seek to identify the
protective effects of toilets and food markets against adverse “treatments” that cannot be
experimentally assigned, but are experienced randomly by children in utero and during the
first year after birth. In each subsample, we employ OLS with the following base
specification:Yi = β0 + β1t NDVIit + δiZi + ui Our notation is the same as for Eq. (1),
except that the vector of NDVIit conditions is the average value of NDVI in each three-
month period t, from the first trimester of pregnancy through the first year after birth
when the child is aged 0–2 months, 3–5 months, 6–8 months, and 9–11 months. All Zi control
variables are the same as in our exploratory regressions, first using both types of age
controls, and then using only the more flexible quadratic approach to controlling for the
child’s age at the time of measurement. Our hypothesis is that the β1t coefficients of
significance in the whole sample (Table 4) become insignificant among households with
toilets (Table 5) and in districts with more food market activity (Table 6). We conduct
this difference-in-differences test using a split sample approach to gain maximum
flexibility for the coefficients on each regressor. The test is powered by a large sample
size achieved through merging two DHS rounds, and a large magnitude of the baseline β1
effects which could be brought to zero by sanitation and food markets. The results of
Table 4 are similar using either the flexible specification in columns 1, 3, and 5, or the
linear specifications in 2, 4 and 6. In both cases, higher NDVI in the second trimester of
pregnancy is associated with greater attained heights, but only for boys. Girls have lower
attained heights when NDVI is higher in the first three months after birth. Boys also have
lower attained heights when NDVI is higher in months 3–5 after birth, but only in the less
flexible functional form for age at measurement used in column 4. The magnitudes of
effects are quite large. Coefficients shown in Table 4 are scaled per 1000 points of NDVI,
so based on our preferred specifications in columns 3 and 5, each 100-point change in NDVI
experienced by boys in midgestation is associated with an 0.088 difference in HAZ—almost
as large as the 0.107 difference associated with each quintile of household wealth. For
girls, each 100-point change in NDVI experienced during the first three months after birth
is associated with a 0.054 difference in HAZ, which is almost half of the 0.112 difference
associated with each quintile of wealth. Coefficients on wealth and other control
variables are similar in direction and significance for both boys and girls, except that
the magnitude of coefficients is somewhat larger for boys, suggesting greater
susceptibility to variables such as altitude and maternal age. Turning to the effects of
NDVI on households with and without toilets, from Table 5 we observe the predicted
heterogeneity in effect sizes and significance. In households without toilets,
fluctuations in NDVI significantly affect males only in utero (column 3) and significantly
affect females only in the first three months after birth (column 5). Households with
toilets are largely immune to the effects of NDVI fluctuations at any stage of early child
development. Effect sizes for the subsample without toilets are larger than for the
country as a whole: a 100-point change in NDVI during the second trimester of pregnancy
affects boys’ heights as much as the equivalent of 1.2 quintiles of wealth, while a
100-point change in NDVI during the first three months after birth affects girls’ heights
as much as the equivalent of 1.6 quintiles of wealth. However, those effects completely
disappear in households with toilets. The effects of NDVI on children’s height in
districts with higher or lower levels of food market activity (shown in Table 6) reveal a
murkier picture. In the low-market-use districts, girls are susceptible to NDVI
fluctuations only in their first three months after birth, and boys are susceptible to
NDVI fluctuation in their second trimester of gestation, but these subsamples also show a
significant correlation with NDVI during the period of complementary feeding (six to eight
months of age). This particular correlation holds true for boys in districts with low food
market use, and for girls in districts with high food market use. This could be a spurious
correlation arising by chance in this sample, in part because these two periods in a
child’s life occur in the same season in successive years, so the two NDVIs are highly
collinear. Effect sizes for the main results are roughly similar here as in the previous
table. For boys in districts with low food market participation, a 100-point change in
NDVI in midgestation has an effect size similar to 1.5 quintiles of wealth; for girls, a
100-point change in NDVI in the three months after birth has a smaller effect, similar to
about 0.5 quintiles of wealth.

<hs>  Robustness checks</hs>
  ~~~~~~~~~~~~~~~~~

To test the robustness of our results, we look for artifacts of the method by checking
whether our regressions generate more statistically significant results than would arise
by chance. These placebo regressions use the same data as our main results in Tables 5 and
6, with dependent variables that were determined long before the NDVI fluctuations
occurred, so no causal effect is possible. These variables consist primarily of maternal
characteristics (columns 1–6) plus household wealth and urban or rural location (columns 7
and 8). The base rate of entirely spurious placebo effects is proportional to p-values;
for example, one tenth of the effects appears significant at a p-value of 10 percent.
Table 7 reveals that, among the 7 × 8 = 56 distinct placebo “treatments” tested on each
age-group, only five effects arise with a p-value < 0.1, four effects with a p-value <
0.05, and one with a p-value < 0.01. The number and pattern of significant coefficients in
Table 7 correspond to the frequency of significant correlations that would be expected to
occur by chance alone, and there is no time-related pattern to these correlations, as each
occurs at a different stage of child development. Because our placebo regression tests
used the same data and model structure as Tables 5 and 6, the clear pattern that we
observe for NDVI treatment effects on child height is very likely to be a robust result of
causal mechanisms.

<h>CONCLUSIONS</h>
-----------

The objective of this study is to identify the influence of early-life agroclimatic
conditions on children’s attained heights in Nepal, and to test for the protective effects
of household sanitation and food markets. In so doing, we find clear heterogeneity in
vulnerability to changes in NDVI: boys are most affected by agroclimatic conditions during
their second trimester of gestation, whereas girls are most vulnerable in the three months
after birth. These findings are consistent with biomedical studies of sex-specific fetal
development and socioeconomic studies of gender bias in child care. Both kinds of
vulnerability are eliminated in households with toilets, and greatly reduced in districts
that have more active use of food markets. The magnitude of fluctuations against which
sanitation and food markets are protective is very large: on average, in households
without toilets, for boys each 100-point variation in NDVI during the second trimester of
gestation is associated with as much difference in attained height as conferred by 1.2
quintiles of household wealth, and for girls that same variation during the first three
months after birth is associated with a difference in height equivalent to 1.6 quintiles
of household wealth. The average seasonal change in NDVI from peak to trough in Nepal
during the 2000–2011 period is approximately 200 points in the Mountains and Hills regions
and 300 points in the Terai (lowland) region. The resulting difference in attained height
between the most and least favorable times of year depends on location but is similar to
the differences associated with about one to three quintiles of wealth. To test the
internal validity of these findings, we conducted a number of placebo regressions that
revealed no significant artifactual correlations that could have resulted from selection
effects in birth timing. Heterogeneity in response to agroclimatic conditions provides
important clues as to the causal mechanisms involved, and valuable guidance regarding the
targeting of interventions. Our results are consistent with the premise that household
sanitation protects children against fecal–oral transmission of disease, while food
purchases made possible by more robust food markets protect children against fluctuations
in local food production. Thus, policy interventions to promote sanitation and strengthen
food markets could help protect children against adverse conditions in the future, helping
them to grow up healthy despite the effects of climate change. Our research design
exploited random exposure to varying agroclimatic circumstances in relation to birth
timing. To detect selection effects, we test for the effects of socioeconomic status on
month of birth and found no correlations. We also use a series of placebo regressions to
test whether our research design generates spurious correlations, and find only the
expected base rate of noncausal statistical significance. These empirical tests increase
confidence in the robustness of our results for the Nepali context. The main limitation of
our study concerns the protective effects of sanitation and food markets, as household
toilets and market activity were not randomly assigned. Our regressions control for
observable influences on child height, such as household wealth, parental education,
maternal BMI, and altitude as well as district fixed effects. Violations of the parallel-
trends assumption behind our difference-in-differences design would involve other factors
that make households less vulnerable to agroclimatic conditions, such as cultural
differences. For example, perhaps households with toilets and in districts with stronger
food markets have access to more effective social insurance than the average household
with similar levels of observable control variables. While the large protective effects
found in our data are plausibly explained by differences in fecal–oral disease
transmission and food consumption smoothing, cultural differences or other unobserved
factors cannot be ruled out without conducting large-scale, randomized trials. Future work
could extend our results using other natural experiments in observational data, perhaps
over longer periods and more countries, or refining the measurement of agroclimatic
conditions and the timing of exposure. This study confirms that exploiting natural
experiments can be of great value in identifying the periods in utero and during infancy
when child development is most at risk, and extends previous results to reveal the
socioeconomic conditions that are most able to protect children against those risks. These
results point to the power of investments in maternal health during pregnancy to protect
boys, and in immediate postnatal care to protect girls, as well as the value of sanitation
and food markets for building resilience against variation in agroclimatic conditions.

<h>FUNDING</h>
-------

This project was supported by the United States Agency for International Development
through the Feed the Future Innovation Lab for Nutrition [grant number AID-O-AA-1-1-00005,
for work by WAM, PM and GES], and by the Bill & Melinda Gates Foundation through the
International Food Policy Research Institute [project number 301052.001.001.515.01.01, for
SAB and WAM].


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<ART>Credit crunches and credit allocation in a model of entrepreneurship
====================================================================

Authors: Marco Bassetto, Marco Cagetti, Mariacristina De Nardi
DOI: 10.1016/j.red.2014.08.003
Year: 2015  |  Pages: 53-76
ASJC codes: 2002
Keywords: Borrowing constraints, Credit allocation, Credit crunches, D58, E21, E22, E32, E44, E62, Entrepreneurship, Wealth inequality

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We study the effects of credit shocks in a model with heterogeneous entrepreneurs, financing constraints, and a realistic firm-size distribution. As entrepreneurial firms can grow only slowly and rely heavily on retained earnings to expand the size of their business, we show that, by reducing entrepreneurial firm size and earnings, negative shocks have a very persistent effect on real activity. In determining the speed of recovery from an adverse economic shock, the most important factor is the extent to which the shock erodes entrepreneurial wealth.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The recent turmoil in financial markets has had deep consequences for the allocation of
credit within the economy. Access to credit is particularly important for nascent and
growing firms, for which it is much more difficult to rely only on retained earnings as a
source of financing. In this paper, we study the effects of various types of financial
shocks in a model with two nonfinancial sectors: a corporate sector, primarily composed of
mature firms, and an entrepreneurial sector, whose leverage is limited by its inability to
fully commit to repay debts. The constraints generate a large, and realistic, dispersion
in firm size, and limit the rate at which entrepreneurial firms can grow. We build on the
entrepreneurship model of Quadrini (2000) and Cagetti and De Nardi (2006, 2009), and
introduce a financial intermediation sector that channels resources from savers to users
of capital. Both entrepreneurs and corporate firms require access to intermediated funds.
The reliance of entrepreneurs on intermediaries is one of the parameters used in our
calibration and is most associated with matching the ratio of the wealth of entrepreneurs
to that of workers. We calibrate directly the reliance of corporate firms on outside
funding to match data from the flow of funds. Our main experiment considers the effects of
an increase in the cost of channeling funds through intermediaries, which increases the
cost of borrowing and, in general equilibrium, also depresses the rate of return earned by
savers. This shock can be the result of either a negative productivity shock in the
financial intermediation sector, or the destruction of capital specific to this sector
(e.g., the loss in value of mortgage-backed securities). For the parameters that best
match our target moments, we find that entrepreneurial firms are affected to a deeper
extent than corporate firms. To the extent that entrepreneurial firms tend to be smaller,
this is in line with the empirical findings of Gertler and Gilchrist (1994). When
intermediation costs return to their steady-state levels, both entrepreneurs and corporate
firms stage an initial rebound, but the path to a full recovery is then slow. The wealth
accumulation of the entrepreneurs is affected in a very persistent way. Negative credit
shocks reduce firm size, and, because entrepreneurial firms can grow only slowly, limit
the speed at which firms return to their previous scale when the shocks subside. This slow
transition is characterized by more capital misallocation and, hence, lower output than in
steady state. A key prediction of our model is that the effects of adverse shocks are more
persistent on small businesses. There is some evidence showing that this is the case.
Credit flows to small and large businesses after the financial crisis have behaved in very
different ways. According to the Financial Accounts of the Unites States, credit flows to
both corporate and noncorporate firms (the latter mostly small businesses) dropped sharply
during the financial crisis. However, credit flows to corporations resumed relatively
early in 2010 and went back to healthy levels by 2011, as corporate firms could access
various credit markets (such as the bond market). Credit to noncorporate businesses
continued to decline through 2010 and started rising only slowly thereafter. The same
pattern emerges markedly for the recession of 1990–91, and, to a lesser extent, for most
recessions in the past 50 years, as documented in Fig. 1. In turn, credit availability and
credit flows have an impact on firms' growth. Chodorow-Reich (2014) shows that firms that
had banking relations with less healthy banks not only had more difficulty obtaining
credit after the crisis, but saw larger declines in employment. Interestingly, this effect
is larger for smaller firms. Similarly, according to surveys conducted by the National
Federation of Independent Business (NFIB), the crisis had a long-lasting impact on small
firms' investment plans. The net percentage of firms that planned capital outlays and that
of firms that anticipated business expansions plummeted during the recession and has
increased only slightly in recent years, a much smaller recovery than that seen in
aggregate data on investment.1 A similar pattern appears in the previous two recessions.
These indexes dropped sharply during the recession, but returned to their pre-recession
levels more slowly than aggregate data on investment would suggest. Our model is also
consistent with the differential behavior of employment at firms of different sizes during
the latest recession and recovery, documented also by Siemer (2013). Employment at smaller
firms fell more sharply than at larger firms during the recession, and, since then, the
ratio of employment at small firms (relative to large firms) has remained depressed and
hasn't returned yet to pre-recession levels. In our model, an increase in intermediation
costs also generates an endogenous tightening of borrowing constraints, as entrepreneurial
activity becomes less profitable and the outside option of absconding part of the capital
becomes comparatively more attractive; this channel accounts for about 50% of the drop in
entrepreneurial firm size. Government policy interacts with the financial disruption. We
study two aspects of this interaction. First, the recession initiated by the financial
shock creates a shortfall in the government budget. If income taxes are raised to finance
this shortfall, they constitute a new, independent drain on entrepreneurial profits; this
drain can be even bigger than the financial shock itself, leading to an even longer
recovery. Second, we analyze the effects of a government-targeted intervention in
financial markets that drives a wedge in the cost of funds across different classes of
borrowers. Our experiment is closest in spirit to the U.S. Treasury's guarantee of money
market mutual funds (and implicitly of the underlying commercial paper): We consider a
case in which the government is able to completely and costlessly insulate the corporate
sector from the shock.2 This guarantee is helpful in reducing the depth of the recession,
but it does nothing to improve the recovery, as it concentrates the shock in the sector
that is most vulnerable in the long run. We contrast the effects of our baseline shock
with alternative scenarios, such as a collateral shock, that makes it harder for
entrepreneurs to pledge future repayment of debt, similar to Jermann and Quadrini (2007),
or a traditional shock to total factor productivity (TFP). We find that the response to
these shocks may be quite similar, to the extent that the balance sheet of entrepreneurs
is hit in a similar way; the evolution of this balance sheet is the key element that
affects the speed of the recovery. In our set-up, all these shocks have a very persistent
effect on real activity.

<h>RELATED WORKS</h>
-------------

Many works incorporate credit-market frictions in macroeconomic models but, rather than
studying the direct effect of shocks to these frictions, they focus on how these frictions
affect aggregate investment and help generate and amplify business fluctuations. Among the
earliest and most influential contributions, Bernanke and Gertler (1989) introduce agency
problems such as costly state verification in a dynamic general equilibrium set-up, and
Kiyotaki and Moore (1997) further illustrate the impact of collateral constraints and
their interaction with asset prices and firms' net worth. In both papers, credit
imperfections link investment decisions to the firms' balance sheets and generate a
“financial accelerator” that amplifies and propagates shocks to the macroeconomy. The
recent financial crisis has given further impetus to this literature, highlighting both
the many channels through which credit market imperfections can affect real activity and
the possible effects of government interventions to improve the functioning of credit
markets and the flow of funds between borrowers and lenders. For a review of this
literature, see Bernanke et al. (1999) for earlier contributions and Gertler and Kiyotaki
(2010), Brunnermeier and Sannikov (2014), and Krishnamurthy (2010) for more recent ones.
Here, we only mention a few of the papers most related to our work. We model several types
of financial frictions. Financial intermediation (and more in general frictions in credit
markets) introduces a wedge between the returns to lenders and the cost of capital to
borrowers, a wedge related to the spread between liquid and easily intermediated
securities such as Treasuries and corporate bonds. These credit spreads vary over time and
their level and variation have been shown to be empirically correlated to and potentially
key to understanding output fluctuations (for instance, Gilchrist et al., 2010; Christiano
et al., 2010; Adrian and Shin, 2010). Their role has been highlighted, among others, by
Hall (2011), who shows that in a simple representative-agent economy, credit spreads
(including those for households) are powerful determinants of economic activity and can
generate fluctuations of the magnitude of those seen in the recent crisis, and by Curdia
and Woodford (2010), who study how monetary policy rules should respond to shocks to
credit spreads. We also find that spreads have a significant impact on aggregate output
during a credit crisis; by themselves, spreads have a fairly short-lived effect in our
model economy. It is a different source of frictions that propagates the effect of spreads
and generates a very persistent drop in output. Among borrowers, we explicitly distinguish
corporate and entrepreneurial firms, since these two types of firms react to shocks in
different ways in the data, and credit disruptions are likely to have a differential
impact on the two (see, for example, Quadrini, 1999). We model credit frictions to
entrepreneurs as endogenous borrowing constraints arising from imperfect enforceability of
debt contracts (as in Kehoe and Levine, 1993; Alvarez and Jermann, 2000). In this set-up,
credit availability to entrepreneurs depends on their balance sheet and their available
collateral. The presence of limited commitment slows the growth of nascent firms and links
it to the entrepreneurs' cash flow. It is this channel that propagates the initial
financial shock in our model and is responsible for our main results. Our paper is thus
also closely related to Khan and Thomas (2013), who examine the effect of capital
misallocation that results from a collateral requirement shock in a real business-cycle
model with heterogeneous firms and capital rigidities. Compared to their work, we focus
more closely on small entrepreneurs that own their firm and thus face a consolidated
resource constraint to finance investment and consumption. For these entrepreneurs,
rebuilding the firm's balance sheet comes directly at the expense of their own
consumption, which slows down the adjustment more than in the case of a corporate firm
owned by diversified shareholders. The differential impact of credit frictions on
businesses of different sizes has been shown to be useful in explaining a variety of
phenomena, for instance firm-size distribution (Athreya and Akyol, 2009; Monge, 2009),
firm dynamics (Albuquerque and Hopenhayn, 2004), macroeconomic fluctuations (Cooley et
al., 2004; Jermann and Quadrini, 2012), and growth (Buera and Shin, 2013). More broadly,
the interaction between frictions, entrepreneurship, and inequality is crucial to
understanding the response to macroeconomic shocks (Jermann and Quadrini, 2007), the
effect of certain government policies (Cagetti and De Nardi, 2009; Meh, 2005; Kitao,
2008), and asset pricing (Heaton and Lucas, 2000; Roussanov, 2010; Covas and Fujita,
2011). Shourideh and Zetlin-Jones (2012) report that as much as 90% of investment by
private businesses is financed by outside funding. In our economy too, a substantial
fraction of small-business investment is undertaken with borrowed funds, although this
number is between 50% and 75%. Compared to their work, we have different definitions of
businesses: We look at self-employed entrepreneurs who actively manage their business,
whereas they focus on the universe of private businesses. For our class of entrepreneurs,
the distinction between personal assets and business assets is tenuous as, for example,
private assets are frequently used as collateral for the business.

<hs>  Credit</hs>
  ~~~~~~

External financing to both entrepreneurs and non-entrepreneurial firms is provided by
competitive financial intermediaries. The intermediaries borrow funds from workers (and
possibly entrepreneurs, though in equilibrium almost all entrepreneurs will be credit
constrained and will invest all their wealth in their own firm). The entrepreneurial
demand for borrowed funds arises endogenously in the model. As in Kehoe and Levine (1993),
entrepreneurs are subject to borrowing constraints that are endogenously determined in
equilibrium and stem from the assumptions that contracts are imperfectly enforceable.

<hs>  Government and taxation</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

We model progressive taxation of total income as in Cagetti and De Nardi (2009) and use
their parameter estimates. As a first pass, we abstract from the tax implications of
corporate finance decisions by assuming that corporate income taxes are zero and that
capital gains are taxed as regular income.4

<hs>  Households</hs>
  ~~~~~~~~~~

An old entrepreneur who is still able to run a business can decide to keep the activity
going or retire, while a retiree cannot start a new entrepreneurial activity.

<h>CALIBRATION</h>
-----------

In this section, we describe the parameters taken from the literature or estimated outside
of the model (Table 1), and the moments we use to calibrate the remaining parameters
(Tables 2 and 3).

<hs>  Non-calibrated parameters</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~

The coefficient of relative risk aversion σ, the capital share in the non-entrepreneurial
Cobb–Douglas production function α, and the depreciation rate δ are set to values commonly
used in the literature (for instance, respectively, Attanasio et al., 1999; Stokey and
Rebelo, 1995; Gollin, 2002). The probabilities of aging and of dying are such that the
average length of working life is 45 years and that of retirement is 11 years. We assume
that the logarithm of the workers' income is an AR(1) process and approximate it as a
5-point Markov chain using the method in Tauchen and Hussey (1991). The autocorrelation
coefficient and the variance of the error term for the AR(1) process are chosen to obtain
a correlation coefficient of 0.95 (among others, Lillard and Willis, 1978) and a Gini
coefficient for earnings of 0.38 (Huggett, 1996; De Nardi, 2004). The Social Security
replacement rate is 40% of average gross income (see Kotlikoff et al., 1999). The steady-
state ratio of government spending to GDP is set to 18.7%, and the tax rate on consumption
is 11%. All of these parameter choices are discussed in Cagetti and De Nardi (2009). We
set the steady-state financial intermediation cost to obtain a 1.5% spread between the
interest rate paid by borrowers and that received by lenders. This is calibrated to the
historical average of the spread between Baa-rated companies and Treasuries. In our model,
both public and private debt are risk free, and the spread is entirely due to the special
liquidity role of Treasuries, which are assumed not to require any intermediation. For
this reason, we choose to match our private borrowing rate to an empirical counterpart
that features low default risk but is also unlikely to carry any liquidity premium (see
Krishnamurthy and Vissing-Jorgensen, 2012, for more discussion). As a comparison with
other securities, the average spread between AAA-rated corporate bonds and Treasuries is
about 1.25% and that between BBB-rated bonds and Treasuries is about 2.2%. The parameter
ξ, the constraint on debt financing, is the average ratio of total corporate debt to the
value of corporate tangible assets, a ratio equal to about 0.34 in the Flow of Funds
Accounts. Corporate debt includes commercial paper, corporate bonds, mortgages, and other
loans; tangible assets include equipment and software (at replacement cost), structures
(at market value), and inventories. The ratio has generally been increasing since the
beginning of the data in 1950, from below 0.25 during the 1950's to values near or above
0.5 in recent years. This ratio jumped to 0.58 immediately after the financial crisis, as
the crash in commercial real estate prices sharply reduced the value of tangible assets,
but since 2009 the ratio has been trending down toward pre-recession norms. For the other
parameters, we take a ratio of government expenditures to GDP of 18.7% (NIPA data), a
consumption tax of about 11% (Altig et al., 2001), and a level of government debt that,
given the equilibrium interest rate, yields an average ratio of total interest payments to
GDP of 3% (Altig et al., 2001).

<hs>  Calibration targets</hs>
  ~~~~~~~~~~~~~~~~~~~

In previous work, Cagetti and De Nardi (2009) have discussed the relevant empirical
counterpart to the concept of entrepreneur in this model. Our entrepreneurs are the self-
employed business owners that actively manage their own firm(s). We identify them in the
SCF as those that declare that they are self-employed, that they own a business, and that
they actively manage it. In total, we calibrate nine parameters. We use the first seven
parameters to target the following moments: the capital–output ratio, the fraction of
entrepreneurs in the population, the fraction of entrepreneurs exiting entrepreneurship
during each period, the fraction of workers becoming entrepreneurs during each period,7
the ratio of median net worth of entrepreneurs to that of workers, the fraction of people
with zero wealth, and the fraction of entrepreneurs hiring workers on the labor market. We
choose the other two parameters to match the revenue from estate and gift taxes and the
fraction of the estates that pay estate taxes. Table 2 reports the target values from the
data and the values generated from our model; Table 3 reports the parameter values used in
our calibration. For the capital–output ratio, we use the Federal Reserve Board Flow of
Funds Accounts. We define capital as tangible assets excluding consumer durables, federal,
state, and local government assets. The measure thus includes equipment and software,
structures, both residential and nonresidential, and inventories. Equipment and software
is measured at replacement cost; structures are measured at market value (except
nonresidential structures owned by the financial sector, for which market value
information is not recorded). With this definition, the ratio for the available years
(1960–2009) is 2.96. Excluding the data after 2000, years that experienced first a large
increase and then a drop in house values, the ratio is slightly smaller, about 2.89. The
fraction of entrepreneurs in the population, the probability of entering and exiting
entrepreneurship, the ratio of the median wealth of an entrepreneur to that of a non-
entrepreneur, and the fraction of entrepreneurs hiring workers are computed from the 1989
Survey of Consumer Finances (other waves give similar results). We compute the transition
matrix between entrepreneurship and non-entrepreneurship by looking at households that are
present in two consecutive surveys. The fraction of the population at zero wealth, also
computed from the SCF, is somewhat sensitive to the exact cutoff point (whether exactly
zero, or some positive but small amount such as $100). This fraction varies from roughly
7% to 13%. The percentage of entrepreneurs hiring workers (besides themselves and,
possibly, their spouse) is also computed from the SCF. We do not use the statutory
exemption and tax schedule to model the estate tax. As explained in Cagetti and De Nardi
(2009) and in the references therein, the effective tax rate can differ substantially from
the statutory one. We thus calibrate the exemption level and the (flat) tax rate above the
exemption to match the percentage of estates that pay an estate tax (2%) and the total
amount of revenues of estate and gift taxes (about 0.2–0.3% of GDP).

<h>A DISCUSSION OF THE STEADY STATE, THE FIT OF THE MODEL, AND ITS MECHANISMS</h>
--------------------------------------------------------------------------

As shown in Cagetti and De Nardi (2006, 2009), our model of entrepreneurship, although
simple, matches very well the wealth distributions of both entrepreneurs and workers. In
the presence of borrowing constraints, this is very important to determine the response to
financial shocks for both the whole distribution of entrepreneurs and for the important
macroeconomic aggregates. Figs. 2 and 3 compare the distribution of net worth for workers
and entrepreneurs generated by the model and in the actual SCF data and confirm that the
model generates the long upper tail of the wealth distribution that is observed in the
data for the whole population, as well as the large wealth holdings concentrated in the
hands of a few entrepreneurs. In our calibration, the entrepreneurial sector employs about
57% of the capital, a little over the value reported by the Small Business Administration
(which is about 50%).8 It also employs 33% of the efficiency units of labor in the
economy; in the data, the Small Business Administration reports that the entrepreneurial
sector employs almost 50% of the workers in the economy; in the data, larger (corporate)
firms tend to pay more, which helps in closing this gap. Table 4 displays the distribution
of labor hiring by entrepreneurial firms. The first line is computed from the 2007 SCF
data, which is the last survey year before the crisis (the numbers from previous years are
very similar). The question asked in the SCF is how many workers the entrepreneurs hire in
their firm (we exclude the entrepreneur and his or her spouse). To compare it with the
model, we assume that the average employee of the entrepreneurial firm (up to the 95%
quantile) lies at either the 33rd percentile (second line) or the median of the efficiency
distribution (third line) and that he works full time. Given that some of the employees in
the SCF data will be part time, we conclude that the distribution of hiring by
entrepreneurial firms in the model matches the one in the data reasonably well. In the
data, entrepreneurs are much richer than workers, and their saving rate does not quickly
decline with wealth. To match these facts, the calibration implies borrowing limits that
are tight compared with the optimal firm size, hence the growth process of entrepreneurial
firms is slow. This plays an important role for the response of the economy to various
shocks, to which we now turn.

<h>COMPUTING TRANSITIONS: THE SHOCKS AND THEIR EFFECTS</h>
---------------------------------------------------

Throughout the experiments below, we start the economy at the deterministic steady state
in period 1. We trace the response to a temporary change in the technology or credit
parameters (a “shock”) that lasts for three years, from period 2 to period 4. This path is
known by all agents at the beginning of period 2, before any decision is made.

<hs>  Negative technology shock in the intermediation sector</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We consider the effect of a shock that increases ϕ from 1.5% to 3.5% for three years.10
This is a way of capturing either of two alternative shocks: More monitoring is necessary
to ensure loan performance due to the financial turmoil. ϕ stands in as payments to a
factor that is fixed in the short run and that is temporarily depleted. As an example,
suppose that banks face capital requirements and that some initial losses wipe some of the
capital out, constraining the banks' ability to offer additional intermediation services.
In this case, the increase in ϕ would reflect the additional reward for the scarcer
banking capital.11 Fig. 5 shows the effect of the financial intermediation shock on the
number of entrepreneurs and their average firm size. The fraction of entrepreneurs drops,
particularly when taxes adjust, but this margin is not very persistent: when
intermediation costs and taxes are back to normal, entrepreneurs quickly reenter the
market. This is because the minimum firm size that makes entry profitable is small, and
potential entrepreneurs can save to reach that point quickly. Average firm size also
drops; this effect is bigger and much more persistent. The intermediation cost reduces the
entrepreneurs' cash flow and their ability to retain earnings to foster their business'
growth. Since both the wealth distribution and the distribution of assets across firms
that we match are very spread out, our model implies a very gradual growth of firms, with
almost no entrepreneur attaining sufficient wealth that borrowing constraints cease to
bind. It follows that any negative shock has almost a permanent effect on each
entrepreneur and its aggregate impact vanishes fully only when each entrepreneur loses his
ability and closes the firm. As soon as the shock is over, firm growth resumes, but at a
slow pace dictated by the tight borrowing limits. The alternative ways in which taxes,
spending, and interest rates adjust across the three experiments reveal important
differences. Consider first the cases in which taxes are held fixed, and government
spending acts as a residual. Fig. 6 plots the borrowing and lending rates for the case in
which the lending rate is held fixed (a small open economy) and that in which the capital
market clears. During the periods of the shock, borrowing rates spike higher when savers
have the opportunity of earning a fixed rate abroad. As a consequence, in Fig. 5, average
firm size drops more when lending rates are held constant (solid line) than when the
effect of the shock is spread between borrowers and savers, as in general equilibrium
(dashed line). The difference between partial and general equilibrium reverses after the
shock is over. The shock triggers a reduction in aggregate capital; in general
equilibrium, the resulting higher interest rates impair the entrepreneurs' ability to
rebuild their balance sheet and lead to a slower recovery in firm size. The differences
between the solid and dashed lines in Fig. 5 are minor compared with the differences
between either of those lines and the dotted line, which represents the case in which the
government balances its budget by increasing taxes rather than cutting government
spending. To balance the budget, the government needs an increase in the tax rate of about
1.5% for nine years. The government imbalance does not have a large impact on the depth of
the initial recession, but it causes a prolonged slump once the fiscal adjustment takes
place. In our model, taxes work very similarly to the intermediation shock that is the
original disturbance: Both changes deprive entrepreneurs of the cash flow which is the
source of growth for their firms. As a consequence, when taxes increase, the average firm
size of entrepreneurs suffers from a gradual contraction whose cumulative effect is
several times larger than the original, shorter-lived shock. The gradual erosion of
entrepreneurial wealth has a corresponding effect on GDP, both because it depresses
capital accumulation (through lower interest rates) and because it shifts capital and
labor towards less productive uses in the corporate sector. In the short run, investment
takes a greater hit than consumption. However, as the period of high taxes drags on, a
smaller firm size implies greater marginal product of capital, which acts as a
countervailing force and prevents further falls in investment. In contrast, the impact on
consumption, which is initially more muted, compounds over time, so that, by the end of
the period of high taxes, consumption and investment have dropped approximately by the
same amount relative to their steady-state level. The recovery from the double shock of an
increase in the intermediation cost and the subsequent response in taxes is delayed
compared with what happens when government spending is cut, and it starts from a weaker
position. Fig. 7 compares value added in the entrepreneurial vs. the corporate sector of
the economy. Since both sectors use capital intermediated by the financial sector, their
value added drops when the cost of accessing the intermediaries' services increases. For
our calibration, entrepreneurs are more reliant on financial intermediation, and the drop
in their value added is twice as large as that for the corporate sector. In period five
the borrowing-cost shock is over and the effect reverses. In this period, the value added
in the entrepreneurial sector grows faster than in the corporate sector; nonetheless,
entrepreneurs do not recover fully, while the corporate sector stages a full recovery. The
difference across the two sectors is due to the nature of the credit frictions faced by
the two types of firms. Entrepreneurs are primarily constrained by their net worth, which
can only be rebuilt slowly, whereas corporate firms curtail their investment only because
of the additional cost of borrowing in Eq. (8), a period-by-period cost that returns
almost to normal as soon as intermediation costs revert to their steady-state level. From
period five, the two economies in Fig. 7 diverge. When (wasteful) government spending acts
as the residual (left panel), no further shock perturbs the entrepreneurs' wealth
accumulation, and the economy immediately starts on a path of slow convergence back to the
steady state. In contrast, when taxes adjust, their effect on the entrepreneurs' balance
sheet tightens the constraint on entrepreneurial firm size and results in a reallocation
of resources from entrepreneurs to corporate firms. Due to computational limitations
related to the endogenous borrowing constraints, our model features an inelastic labor
supply, and thus it cannot capture the decline in labor occurring during the downturn.
However, we can analyze the relative allocation of labor across the two sectors, which we
show in Fig. 8. This picture mirrors what we observed for output: The recession caused by
the financial shock shrinks the share of employment at entrepreneurial firms, in line with
Gertler and Gilchrist (1994), who observe that small firms are more sensitive to the
business cycle. Our results are also in line with what Moscarini and Postel-Vinay (2012)
find, that small firms grow comparatively faster early in the recovery; this is
particularly clear in the left panel of Fig. 8, where the prolonged slump due to the
increase in taxes is absent. The comparatively fast growth in employment at
entrepreneurial firms is partially compensating for the losses occurred during the
recession, but it is not enough to close the gap in levels: In our model, employment in
the sector remains depressed for a long time.12 Our results about relative employment
levels mimic the Business Employment Dynamics data on employment by firm size published by
the Bureau of Labor Statistics and the results by Siemer (2013). The dataset does not
identify entrepreneurial firms per se, but, as a proxy, we can look at firms by number of
employees. Fig. 9 shows that the ratio of employment at firms with fewer than a certain
number of employees relative to employment at firms with more than the same threshold
number fell sharply during the 2007–2008 recession, indicating that small firms shrank
more than larger ones. In addition, after the initial fall, the ratio has moved up only
slowly, and remains below its pre-recession level even several years into the recovery,
indicating that the effect of the shock is particularly persistent for small firms. Having
analyzed the forces that drive the behavior of our economy, we now turn to their aggregate
implications. Fig. 10 plots aggregate GDP. The increase in intermediation costs (an
intermediate input in our economy) depresses TFP and output during the financial shock.
This is particularly true when lending rates are fixed, since in this case capital moves
out of the economy.13 In general equilibrium, the output drop on impact is mostly driven
by the TFP effect of the shock: The drop in output is close to 3%, with 0.3% being due to
the misallocation of factors. As the net worth of entrepreneurs is eroded, the
misallocation becomes a more prominent force; after the shock is over, the entire
difference between the solid line and the steady state is due to this misallocation,
whereas in general equilibrium (dashed and dotted line) the decrease in capital
accumulation plays a role. When taxes hit the entrepreneurs' ability to accumulate wealth
and grow their own business, the economy fares much worse. This second dip would be less
pronounced with a longer transition period over which taxes are raised; but, of course, in
this case the policy response to the shock would have even more persistent effects. Fig.
11 plots aggregate consumption and investment.14 As in most business-cycle models,
investment bears the brunt of the shock at first. Nonetheless, consumption drops too.
Unlike a pure tightening of borrowing constraints, a shock to financial intermediation
entails real output costs that reduce total available resources from the outset. In
general equilibrium, the behavior of aggregate investment contributes to a slow recovery:
After the initial drop in the periods of the shock, investment never overshoots its
steady-state level. When government spending adjusts, investment merely returns close to
steady state; when taxes further depress wealth accumulation, investment remains 2% below
its steady state several years after taxes have returned to their steady-state level. It
has often been remarked that, during the crisis, credit standards were extremely tight and
businesses found it difficult to access credit at any price (see, for example, the
Quarterly Senior Loan Officer Opinion Survey conducted by the Federal Reserve Board). A
similar effect arises in our model: The increase in intermediation costs is accompanied by
an endogenous tightening of the constraints, because entrepreneurship becomes less
profitable and thus the temptation of terminating the business and absconding with part of
the capital becomes stronger. To illustrate this mechanism, we run an alternative
experiment, where intermediation costs increase by the same amount and duration (2% for
three years), but borrowing constraints are held fixed exogenously at their steady-state
values. Fig. 12 compares the effect of the intermediation shock for exogenous and
endogenous borrowing constraints with government spending acting as a residual. It shows
that the adjustments of the extensive margin are almost exclusively driven by the
tightening of the borrowing limits, which forces potential entrepreneurs to accumulate
more wealth before entry becomes worthwhile. The profit loss from the intermediation shock
leads to smaller firms even with fixed borrowing constraints, but the drop in average firm
size is about half as large. After the shock, the speed of recovery is similar, but the
level from which the economy has to recover is much lower with endogenous borrowing
constraints, so that it takes longer to return to the same level of output. The behavior
of GDP with endogenous vs. fixed borrowing limits (Fig. 13) mirrors the one for the
average size of firms, but quantitatively the tightening of borrowing constraints has a
more muted impact in the periods of the shock. When the shock is active, both
entrepreneurs and corporate firms are subject to it, and holding borrowing limits fixed
only benefits entrepreneurs. After the shock is over, the gap between the two lines
widens, because the persistent effect of the shock is dictated by the evolution of
entrepreneurial wealth, which is less severely impacted when borrowing constraints are
held fixed. Figs. 14 and 15 compare the behavior of entrepreneurial firms and GDP with
endogenous vs. fixed borrowing constraints in the case in which the government raises
taxes to balance its budget. The differences are starker here, because an increase in
taxes drains the profitability of entrepreneurs and generates its own credit crunch if
borrowing constraints are allowed to adjust endogenously.

<hs>  Negative technology shock in the intermediation sector, only for entrepreneurs</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In the wake of the financial crisis of 2008, the government took several actions aimed at
restoring calm in several financial markets. Among the actions that were most successful
ex-post was a blanket guarantee of money market mutual funds, and thus, indirectly, of the
commercial paper of corporate industrial firms that those funds purchased. More generally,
companies with direct access to markets seemed better able to cope than those that were
forced to go through the banking sector.15 Fig. 16 studies the differences between this
experiment and the case of a pure shock to ϕ for the entrepreneurial sector, in the case
of general equilibrium and fixed taxes (with government spending adjusting as a residual).
Since corporate firms are insulated from the shock in this new experiment, entrepreneurs
face stiffer competition in the factor markets, which thins their ranks and leads them to
shrink their firm size more. The recovery is affected by two opposite forces. The greater
hit taken by entrepreneurs slows the return to the steady state. However, aggregate
investment (Fig. 17) drops less when only one sector is hit by the shock, and the
additional capital is beneficial to the recovery. The first force dominates in the short
run, but about five years after the shock the two experiments become quite similar. Fig.
18 displays the value added in the two sectors in response to the shock to ϕ and the
contemporaneous offset through ξ. When the corporate sector is completely insulated, its
size actually expands during the financial disruption, as it poaches workers and capital
from the entrepreneurs. Fig. 19 shows how all of these effects combine to determine
aggregate GDP. Even in the best-case scenario, in which the government intervention
entails no cost, it is successful at reducing the severity of the recession but it has
almost no impact on the recovery. By helping the corporate sector, the government
exacerbates the misallocation of resources due to financial frictions.

<hs>  A shock to required collateral</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Here, we consider a shock that increases the collateral that the entrepreneurs need to
secure their loans. Specifically, we raise the fraction of capital with which
entrepreneurs can abscond (f) from 75% to 80%. We calibrate this shock to have an effect
on aggregate output during the credit crunch that is of similar magnitude of the drop that
we obtained considering a shock to ϕ for the cases of general equilibrium. This can be
seen in Fig. 20.17 Since this shock only affects the entrepreneurial sector, matching the
output drop on impact requires a much deeper contraction in the number of entrepreneurs
and firm size when f increases than the baseline case in which borrowing costs increase
for both entrepreneurs and corporate firms. This can be seen in Fig. 21. It might seem
surprising that the deeper contraction in entrepreneurial firms does not bear bigger
implications for the entrepreneurs' wealth in the recovery phase. The reason for this
result is that a shock to f hits only the marginal profits of the firm: It forces
entrepreneurs to shrink their scale, but it has no effect on their profits for a given
scale of operations. In contrast, an increase in ϕ raises the rental rate of capital paid
by entrepreneurs. This effect applies to all of the capital that they rent and has a
negative effect on their profits even conditioning on their scale of operations.

<hs>  A TFP shock</hs>
  ~~~~~~~~~~~

We finally contrast a credit shock to a TFP shock that hits both the corporate sector and
the entrepreneurial sector. In this case, TFP drops by 2.5% for three years, and
subsequently reverts to steady state. Once again, the magnitude of the TFP drop is chosen
so as to obtain a similar GDP drop on impact in general equilibrium. As Figs. 22 and 23
show, the evolution of the economy under this shock is fairly similar to that of a shock
to ϕ.

<h>CONCLUSION</h>
----------

From the experiments that we ran, we learn three lessons. First and foremost, we find that
it is not the source of the disturbance that determines our economy's speed of recovery,
but rather the way in which the shock affects the profitability of credit-constrained
entrepreneurs. Recovery is slowest in the case of an increase in borrowing rates from
which the corporate sector is shielded (our experiment of Section 6.2). Among our
experiments, this one has the shallowest recession; and yet during the recovery output is
at a similar level as that of the others, in which the economy needs to make up for deeper
drops. When losses are concentrated in the entrepreneurial sector, it takes more time for
entrepreneurs to rebuild their balance sheet. Second, the way public finances adjust in
response to the shortfalls caused by a recession is important. Income taxes are a further
drain on the cash flow available for successful business owners to grow and represent a
further significant drag on the economy. From an efficiency perspective, entrepreneurship
subsidies would contribute to increasing output. It should be noted that this does not
necessarily imply that subsidizing entrepreneurs is an optimal policy. Even if it were
easy to identify the exact counterpart to credit-constrained, highly productive
entrepreneurs, this policy would require taxing workers, who are on average far poorer in
our economy, as in the data, to subsidize comparatively richer business owners, raising
equity considerations. Finally, in an environment with endogenous borrowing constraints,
financial shocks that increase interest costs have two effects. The interest rate increase
represents a direct drain on firms' profits. The indirect effect is that higher borrowing
rates trigger a tightening of credit limits. Hence, for a given contraction in credit,
financial shocks that affect borrowing rates have potentially more severe implications
than pure credit rationing.


<h>REFERENCES</h>
----------

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  [2] Rui Albuquerque, Hugo A. Hopenhayn. Optimal lending contracts and firm dynamics. doi:10.1111/0034-6527.00285
  [3] David Altig, Alan J. Auerbach, Laurence J. Kotlikoff, Kent A. Smetters, Jan Walliser. Simulating fundamental tax reform in the United States. doi:10.1257/aer.91.3.574
  [4] Fernando Alvarez, Urban J. Jermann. Efficiency, equilibrium, and asset pricing with risk of default. doi:10.1111/1468-0262.00137
  [5] Ahmet Akyol, Kartik Athreya. Self-employment rates and business size: The roles of occupational choice and credit market frictions. doi:10.1007/s10436-008-0115-5
  [6] Orazio P. Attanasio, James Banks, Costas Meghir, Guglielmo Weber. Humps and Bumps in Lifetime Consumption. doi:10.1080/07350015.1999.10524794
  [7] Ben Bernanke, Mark Gertler. Agency costs, net worth, and business fluctuations
  [8] Ben S. Bernanke, Mark Gertler, Simon Gilchrist. Chapter 21 The financial accelerator in a quantitative business cycle framework. doi:10.1016/S1574-0048(99)10034-X
  [9] Markus K. Brunnermeier, Yuliy Sannikov. A macroeconomic model with a financial sector. doi:10.1257/aer.104.2.379
  [10] Francisco J. Buera, Yongseok Shin. Financial frictions and the persistence of history: A quantitative exploration. doi:10.1086/670271
  [11] Marco Cagetti, Mariacristina De Nardi. Entrepreneurship, frictions, and wealth. doi:10.1086/508032
  [12] Marco Cagetti, Mariacristina De Nardi. Estate taxation, entrepreneurship, and wealth. doi:10.1257/aer.99.1.85
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<ART>Delta-method inference for a class of set-identified SVARs
==========================================================

Authors: Bulat Gafarov, Matthias Meier, José Luis Montiel Olea
DOI: 10.1016/j.jeconom.2017.12.004
Year: 2018  |  Pages: 316-327
ASJC codes: 2002
Keywords: Directional differentiability, SVAR, Set-identification, Sign restrictions, Unconventional monetary policy

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We study vector autoregressions that impose equality and/or inequality restrictions to set-identify the dynamic responses to a single structural shock. We make three contributions. First, we present an algorithm to compute the largest and smallest value that an impulse-response coefficient can attain over its identified set. Second, we provide conditions under which these largest and smallest values are directionally differentiable functions of the model's reduced-form parameters. Third, we propose a delta-method approach to conduct inference about the structural impulse-response coefficients. We use our results to assess the effects of the announcement of the Quantitative Easing program in August 2010.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

An increasingly popular practice in empirical macroeconomics is to set-identify the
parameters of a structural vector autoregression [SVAR] by means of exclusion and/or sign
restrictions. Most studies working with this type of models have relied on Bayesian
methods to construct posterior credible sets for the structural parameters of interest
(for example, Inoue and Kilian, 2013; Arias et al., 2017; Baumeister and Hamilton 2015). A
practical concern with Bayesian analysis in set-identified SVARs is that posterior
inference continues to be influenced by prior beliefs even if the sample size is infinite
(Poirier, 1998; Gustafson, 2009; Moon and Schorfheide, 2012). This observation has
motivated the study of alternative approaches to inference that dispense with the
specification of a prior distribution over structural parameters that are only set-
identified. There are two existing proposals that characterize the estimation uncertainty
of set-identified structural responses, without postulating a specific prior for the
parameters of the structural model. On the one hand, Granziera et al. (2017) [GMS17] have
proposed a frequentist confidence interval for structural impulse-response coefficients
based on a moment-inequality-minimum-distance framework. On the other hand, Giacomini and
Kitagawa (2015) [GK15] have proposed a robust Bayes credible interval that achieves a
given credibility level regardless of the prior specified over the model’s set-identified
structural parameters. We contribute to the analysis of set-identified SVARs by proposing
a novel delta-method interval for the coefficients of the impulse-response function [IRF].
We show that our delta-method interval is point-wise consistent in level and, under
certain regularity conditions, has asymptotic robust Bayesian credibility of at least the
nominal level. Thus, our inference approach can be interpreted both from a frequentist and
a robust Bayes perspective. We also argue that the computational cost of our procedure
compares favorably with GMS17 and GK15. Broadly speaking, our approach is based on a
closed-form characterization of the endpoints of the identified set and their directional
derivatives. Our delta-method interval – which may be viewed as a generalization of the
pioneering work of Lütkepohl (1990) on delta-method inference for point-identified VARs –
takes the form of a plug-in estimator for the identified set plus/minus standard errors.
The main limitation of our approach is that the delta-method interval is only defined for
SVAR models that impose equality and inequality restrictions on a single structural shock
(e.g., a monetary policy shock). Admittedly, this is problematic, as some popular
applications of set-identified SVARs feature restrictions on multiple structural
innovations.1 In spite of this observation, single-shock set-identified models have been
applied in several empirical studies: for example, to study the effects of monetary policy
on output (Uhlig, 2005), the impact of monetary policy on the housing market (Vargas-
Silva, 2008), the effects of labor market shocks on worker flows (Fujita, 2011), the
effects of exchange rates on aggregate prices (An and Wang, 2012), and the effect of
optimism shocks on business cycles fluctuations (Beaudry et al., 2011). Thus, we think
there is room for our results to have an impact on empirical work. To illustrate the
usefulness of our main results, we estimate a monetary structural vector autoregression
using monthly U.S. data from July 1979 to December 2007 (a sample that deliberately ends a
half-year before the financial crisis begins). The goal of our exercise is to use pre-
crisis data to learn about the responses of macroeconomic variables to shocks that have
effects similar to the ‘unconventional’ monetary policy interventions implemented after
the crisis. We set-identify an unconventional monetary policy [UMP] shock as an innovation
that decreases the two-year government bond rate upon impact, but has no effect over the
nominal federal funds rate.2 We consider two additional sign restrictions on the
contemporaneous responses of inflation and output. Namely, we assume that – upon impact –
neither inflation nor output can respond negatively to a UMP shock. Since the model is
only set-identified, our analysis effectively captures the effects of any historical
economic shock that affected the economy in the same way as an UMP shock. We apply our
delta-method approach to construct a confidence interval for the dynamic responses of
industrial production, inflation, the two-year government bond rate, and the nominal
federal funds rate. We use our delta-method intervals to assess the effects of the
announcement of the second part of the so-called Quantitative Easing program (QE2) in
August 2010. Pre-crisis data turns out to be extremely useful to learn about the post-
crisis response of macroeconomic aggregates to unconventional monetary policy. The
remainder of the paper is organized as follows. Section 2 presents an overview of the main
methodological results in this paper. Section 3 introduces our empirical application,
which is used as a running example throughout the paper. Section 4.1 presents our
algorithm to evaluate the endpoints of the identified set. Section 4.2 establishes the
differentiability properties of the endpoints. Section 4.3 presents our delta-method
approach and establishes its asymptotic frequentist validity as well as its asymptotic
robust Bayesian credibility. Section 5 presents the delta-method intervals for the dynamic
responses to the QE2 program. Section 6 concludes. All of our proofs are collected in
Appendix A. Additional figures and implementation details of different procedures are
collected in Appendix B.

<h>MODEL, SET-IDENTIFYING RESTRICTIONS, AND OVERVIEW OF MAIN THEORETICAL RESULTS</h>
-----------------------------------------------------------------------------

This section presents the baseline SVAR model, discusses the class of set-identifying
restrictions that we consider, and provides an overview of our main methodological
results.

<hs>  Set-identifying restrictions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

A common practice in empirical macroeconomics is to use equality and inequality
restrictions to set-identify the structural IRFs in (2.2). An example of an equality
restriction in a monetary VAR is that prices do not react contemporaneously to monetary
policy shocks. An example of an inequality restriction is that a contractionary monetary
policy shock cannot increase prices. The simple formulation in (2.4) allows the researcher
to incorporate the following identifying restrictions:

<hs>  Overview of the main results</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our delta-method approach is supported by the three results described in the abstract,
which can be summarized as follows:

<h>RUNNING EXAMPLE: UNCONVENTIONAL MONETARY POLICY SHOCKS</h>
------------------------------------------------------

This section introduces our empirical application, which will be used as a running example
to illustrate our assumptions and results. Baumeister and Benati (2013) study a related
identification scheme. They consider a Bayesian SVAR to study an analogous ‘spread’
monetary policy shock that leaves the short-term nominal rate unchanged, but affects the
spread between the ten-year Treasury-bond yield and the policy rate. Outline for the rest
of our paper: We have already presented an overview of our main results and described our
running example. In the remaining part of the paper, we formalize Theorems 1–3 and use
them to conduct inference about the responses to an unconventional monetary policy shock.

     <hss>Assumptions</hss>

        We make two assumptions on the sign and zero restrictions allowed in the model:
        This assumption simply requires that the identifying restrictions do not
        contradict each other.

     <hss>Using the algorithm in the UMP example</hss>

        There are at least two other ways of evaluating the maximum and minimum response
        (although only our algorithm is guaranteed to provide a global solution in a
        finite number of steps). One approach is to simply use a numerical solver (such as
        Matlab’s fmincon) to get the value of the non-linear, non-convex program in (2.5).
        The result in Theorem 1 allows us to avoid the specification of the standard
        tuning parameters for numerical optimization routines (such as initial conditions,
        algorithms for the solver, tolerance levels for the solutions, and number of
        iterations).

     <hss>Assumptions</hss>

        In order to establish our differentiability result we need an additional
        regularity condition. Our key assumption is as follows:

     <hss>Directional differentiability</hss>

        We now state the definition of directional differentiability and present our
        second theorem.

<hs>  Theorem 3</hs>
  ~~~~~~~~~

We now describe the main large-sample assumptions used to establish the frequentist
coverage and the robust Bayesian credibility of our delta-method interval.

     <hss>Assumptions</hss>

        Asymptotic Normality of μ̂T Bernstein–von Mises Theorem

<h>UNCONVENTIONAL MONETARY POLICY SHOCKS</h>
-------------------------------------

In August 2010 the Federal Open Market Committee announced: “The Committee will keep
constant the Federal Reserve’s holdings of securities at their current level by
reinvesting principal payments from agency debt and agency mortgage-backed securities in
longer-term Treasury securities.” This announcement was an important prelude for the
second part of the Quantitative Easing program (QE2) (see p. 244 in Krishnamurthy and
Vissing-Jorgensen (2011) for a detailed discussion). In addition, this announcement
generated a drop in the intraday yield for two- and ten-year treasury bond. In fact, from
the end of July 2010 to the end of August 2010 the 2 year Treasury bond rate fell by 10
basis points. Fig. 4 uses our delta-method approach to construct confidence bands for the
evolution of the levels of the four variables in the monetary SVAR. We fix all the
variables at their level on July 2010 and we trace their evolution (over a 12-month
window) according to the confidence set for their cumulative responses. The motivation for
this exercise is as follows. Suppose that – back in August 2010 – an econometrician is
asked to provide confidence bands for the evolution of IP, CPI, 2YTB, and FF after the
August 2010 announcement of the Federal Open Market Committee (FOMC). The econometrician
observes the realization of the macroeconomic variables from July 1979 until August 2010,
but decides to deliberately ignore the two years of data after the crisis (to avoid
introducing structural changes, stochastic volatility, or any other feature that will
complicate the estimation of the VAR). The econometrician uses the data until December
2007 – one semester before the financial crisis – to conduct delta-method inference on the
cumulative responses to a one standard deviation unconventional monetary policy shock. The
econometrician then uses these cumulative responses to get a rough idea of the evolution
of the variables (in levels) following the announcement of the Federal Reserve in August
2010. The econometrician assumes there is a linear trend for CPI/IP, and ignores sampling
uncertainty coming from the trend estimation in reporting the bands. An ex-post evaluation
of this exercise (over a window of 12 months) is reported in Fig. 4.17 We note that the
observed dynamics for CPI, IP, GS2, and FFR from August 2010 to July 2011 fall within the
bounds motivated by our delta-method interval. We also note that our delta-method interval
misses the observed value at most three out of 12 months, which means that our 68%
confidence set covers each of these variables at least 75% of the time. We also report the
68% Bayesian credible sets. Computational Cost: We close this section with some comments
regarding the computational cost of our delta-method procedure. Most of the work to
compute the endpoints of the identified set and its derivatives is analytical.
Consequently, practitioners can expect the computational burden of our procedure to be
low. We note that the implementation of our delta-method interval in the running example
takes only around .15 s (using a standard Laptop @2.4 GHz IntelCore i7). Comparison with
the Projection Approach: Fig. 6 in Appendix B.1 presents a comparison between the delta-
method approach and the projection approach recently proposed by Gafarov et al. (2016)
[GMM16]. The projection approach has two theoretical properties that we were not able to
verify for the delta-method. First, projection is consistent in level uniformly over a
reasonable class of data generating processes. Second, projection yields valid
simultaneous inference; that is, it covers the whole impulse-response function (across
different horizons and different variables) and not only its scalar coefficients.18 We
note that in our application the projection confidence interval (which is wider than the
delta-method bands) contains the realized value of IP, CPI, 2YTB, and FF for every horizon
under consideration. Comparison with GK Robust Approach: Fig. 7 in the Appendix reports
the robust-Bayesian credible set in Giacomini and Kitagawa (2015). The implementation of
the robust-Bayes credible set (based on 10,000 posterior draws and using our algorithm to
evaluate the endpoints) took around 9106 s.19 Comparison with GSM: Fig. 9 in the Appendix
reports the 68% Bonferroni confidence set of Granziera et al. (2017).20 Appendix A.7.1
describes the algorithm and related computational issues. The computational cost is
approximately 4,000 s on a single core machine for 10,000 grid points. It is hard to
provide a general theoretical comparison of the length of the Bonferroni CS and the delta
method. The efficiency ranking of the two procedures is likely depend on the particular
DGP. One can see that, in our illustrative example, the 68% delta method CS is tighter
than the corresponding Bonferroni CS with the same nominal level for almost all
combinations of the horizons and time series. One possible explanation behind the larger
length of Granziera et al. (2017) is that their procedure is uniformly consistent in level
over the class of GDPs for which the reduced form impulse response functions converge to a
normal distribution. We note that our delta-method is not guaranteed to have this
property.

<h>CONCLUSION</h>
----------

This paper focused on set-identified structural VAR models that impose equality and
inequality restrictions to set-identify only one structural shock. For this class of
models, the endpoints of the identified set have special properties that allow an
intuitive and computationally simple approach to conduct frequentist and (asymptotic)
robust Bayes inference. Specifically, the paper made three contributions: (i) We presented
an algorithm to compute – for each horizon, each variable, a fixed vector of reduced-form
parameters, and a given collection of equality and/or inequality restrictions – thelargest
and smallest value of the coefficients of the structural IRF (see Theorem 1). Our
algorithm did not require random sampling from the space of orthogonal matrices or unit
vectors. Instead, we treated the bounds of the identified set as the maximum and minimum
value of a mathematical program whose solutions we were able to characterize analytically.
Our algorithm can be used outside our delta-method framework (for example, in computing
the maximum and minimum response for the (Giacomini and Kitagawa, 2015) robust Bayes
approach). (ii) We provided sufficient conditions under which the largest and smallest
value of the structural parameters are directionally differentiable functions of the
reduced-form parameters (see Theorem 2). This result also seems to be of interest in its
own right and could be used to explore the frequentist properties of the robust-Bayesian
procedure in Giacomini and Kitagawa (2015). (iii) Finally, we proposed a computationally
convenient delta-method approach to conduct inference for the set-identified coefficients
of the structural IRF. We presented sufficient conditions to guarantee the point-wise
consistency in level and asymptotic robust Bayes credibility of our suggested inference
approach. We note that the delta-method in this paper exploited the structure of the
directional derivative. We illustrated our results by set-identifying the responses of
different U.S. macroeconomic variables to an unconventional monetary policy shock. We used
the theory and methods developed in this paper to assess the effects of the announcement
of the second part of the Quantitative Easing program in August 2010.


<h>REFERENCES</h>
----------

  [1] Lian An, Jian Wang. Exchange Rate Pass-Through: Evidence Based on Vector Autoregression with Sign Restrictions. doi:10.1007/s11079-010-9195-8
  [2] Juan J. Dolado, Helmut Lütkepohl. Making wald tests work for cointegrated VAR systems. doi:10.1080/07474939608800362
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  [7] Shigeru Fujita. Dynamics of worker flows and vacancies: Evidence from the sign restriction approach. doi:10.1002/jae.1111
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  [14] Paul Gustafson. What are the limits of posterior distributions arising from nonidentified models, and why should we care?. doi:10.1198/jasa.2009.tm08603
  [16] Atsushi Inoue, Lutz Kilian. Bootstrapping autoregressive processes with possible unit roots. doi:10.1111/1468-0262.00281
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  [18] Lutz Kilian. Small-sample confidence intervals for impulse response functions. doi:10.1162/003465398557465
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<ART>Disease externalities and net nutrition: Evidence from changes in sanitation and child height in Cambodia, 2005–2010
================================================================================

Authors: Sangita Vyas, Phyrum Kov, Susanna Smets, Dean Spears
DOI: 10.1016/j.ehb.2016.10.002
Year: 2016  |  Pages: 235-245
ASJC codes: 2001
Keywords: Cambodia, Disease environment, Early-life health, Height, Sanitation

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Child height is an important indicator of human capital and human development, in large part because early life health and net nutrition shape both child height and adult economic productivity and health. Between 2005 and 2010, the average height of children under 5 in Cambodia significantly increased. What contributed to this improvement? Recent evidence suggests that exposure to poor sanitation – and specifically to widespread open defecation – can pose a critical threat to child growth. We closely analyze the sanitation height gradient in Cambodia in these two years. Decomposition analysis, in the spirit of Blinder-Oaxaca, suggests that the reduction in children's exposure to open defecation can statistically account for much or all of the increase in average child height between 2005 and 2010. In particular, we see evidence of externalities, indicating an important role for public policy: it is the sanitation behavior of a child's neighbors that matters more for child height rather than the household's sanitation behavior by itself. Moving from an area in which 100% of households defecate in the open to an area in which no households defecate in the open is associated with an average increase in height-for-age z-score of between 0.3 and 0.5. Our estimates are quantitatively robust and comparable with other estimates in the literature.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Child height is an important indicator of human capital and human development, in large
part because of its importance for adult economic productivity and health (Currie, 2009;
Vogl, 2014). This is chiefly because height is determined by health and net nutrition in
the first few years of life, a critical period for cognitive development (Case and Paxson,
2008). In poor countries, the disease environment to which children are exposed and income
are important indicators for adult height (Bozzoli et al., 2009). The importance for
height and child development of early-life health, relative to genetics, is even greater
in these countries compared to richer countries (Martorell et al., 1977; Spears, 2012b).
Recent econometric evidence suggests that exposure to germs from open defecation is an
important determinant of child height in developing countries (World Bank, 2008; Spears,
2013), and epidemiological evidence suggests that potential mechanisms for this
relationship include diarrhea, intestinal parasites, and environmental enteropathy, a
disease of the small intestine. It is therefore important to better understand the
relationship among sanitation, the early-life disease environment, and subsequent child
health and human capital outcomes, especially in countries where practicing open
defecation is widespread. We study the relationship between open defecation and child
height in Cambodia, where 77% of households defecated in the open in 2005 and 63% in 2010.
The primary contribution of this paper is to document what accounts for Cambodian children
growing taller between 2005 and 2010. We show that much of the increase in child height
over this period of time can be statistically accounted for by the increase in sanitation
coverage over the same period. In studying Cambodia, this paper makes three important
contributions to the literature. First, in Cambodia open defecation is particularly
common, representing an enduring development challenge and an unusually threatening
disease environment for children. Second, although the country remains far from
eliminating open defecation or child stunting, Cambodia saw an improvement in child height
from 2005 to 2010, coupled with a decrease in open defecation. This improvement, which was
unusually rapid among developing countries, gives us the opportunity to study any
association that may exist between the two.1 Third, we use decomposition techniques to
examine whether the change in sanitation can statistically account for the improvement in
child height over this period of time. The empirical analysis in this paper is in two
parts. The main question we seek to answer is how much of the increase in child height
from 2005 to 2010 can be statistically accounted for by the reduction in open defecation.
We apply three complementary decomposition techniques: regression analysis to examine
whether controlling for local open defecation eliminates the statistical importance of the
indicator for survey year, a standard linear Blinder-Oaxaca decomposition, and a non-
parametric decomposition. Although open defecation remains common in Cambodia, we find
that its decline over the period studied can account for most or all of the increase in
child height. Before computing decompositions, we first explore the association between
exposure to open defecation and child height over time by combining the two most recent
Demographic and Health Surveys in Cambodia and using panel data methods. This analysis
provides support for the association between sanitation and stunting on which we rely for
computing decompositions. Using urban and rural province part fixed effects, which
isolates the variation within province parts, we find that the geographic areas in which
open defecation decreased by more saw a greater improvement in child height, on average.
In particular, we document negative externalities of open defecation: the rate of open
defecation in the child’s locality is more important for child height than the sanitation
practices of the child’s own household, indicating an important role for policy as
households’ own private demand for latrines may be too low. This preliminary result is
robust to a range of specifications. We test the mechanisms through which we expect open
defecation to affect child height. We show that the association between open defecation
and child height is steeper in urban areas, which is consistent with greater exposure to
fecal pathogens when open defecation occurs in higher density areas, and that there is
also an association between open defecation and child weight, consistent with mechanisms
that affect child growth. We also perform two robustness checks: estimating our model by
isolating the variation within regions in a particular year, and including data from the
Demographic and Health Survey conducted in 2000.

<hs>  Open defecation and child stunting</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

According to WHO and UNICEF Joint Monitoring Program (JMP) statistics for 2015, 13% of
people in the world defecate in the open. Of these roughly one billion people, about 7.5
million live in Cambodia, representing 48% of the country’s population.2 Among developing
countries, open defecation is particularly common in Cambodia, notably more common than in
the rest of Southeast Asia, where 10% defecate in the open, sub-Saharan Africa, where 23%
do, and South Asia, where 34% do. Poor sanitation has important implications for the
health and nutritional status of children, and a sizeable body of evidence in the fields
of medicine and epidemiology demonstrates this link through a combination of three or more
possible mechanisms, the importance of each of which may differ across contexts. These
mechanisms include diarrhea, intestinal parasites, and environmental enteropathy. Checkley
et al. (2004) used a cohort study in Peru to show that safe water and sanitation
practices, which reduced fecal-oral contamination, were associated with fewer diarrheal
episodes and better nutritional outcomes, as measured by height-for-age, in children. A
meta-analysis conducted by Esrey (1996) has shown an effect of sanitation on intestinal
parasites. More recently, researchers have investigated the role of environmental
enteropathy (EE) as another, and perhaps more important, mechanism linking fecal-oral
contamination to malnutrition (Humphrey, 2009). EE is a largely subclinical condition that
is demonstrated by damage to the walls of the small intestine thereby reducing its
absorptive capacity. There is substantial evidence linking markers of EE to lower height-
for-age z-scores (Kosek et al., 2013; Goto et al., 2009; Campbell et al., 2003; Lunn et
al., 1991), and there is now a growing literature linking the sanitation environment to
markers of EE. One recent observational study finds that indicators of EE and malnutrition
are higher among children who live in “dirtier” households, where they are exposed to more
fecal pathogens (Lin et al., 2013). EE may even be at play when clinical conditions like
diarrhea are absent. A recent study in Mali found an effect on child height, but not on
diarrhea, of a randomly assigned Community-Led Total Sanitation program (Pickering et al.,
2015). This paper joins a growing econometric literature documenting effects of open
defecation on child height. Gertler et al. (2015) use experimentally-induced variation in
open defecation from four randomized controlled trials (RCT) of independently conducted
sanitation programs in different countries to find a causal relationship between village
open defecation and child height. An RCT in Indonesia, one of the experiments studied in
Gertler et al.’s meta analysis, shows that a Total Sanitation and Sanitation Marketing
project increased average height of children living in households without access to
sanitation at baseline (Cameron et al., 2013). Another RCT, conducted in Maharashtra,
finds that improvements in sanitation brought about by the Indian government sanitation
program increased average child height (Hammer and Spears, 2015). In India in particular,
econometric studies of a government sanitation program document a link between sanitation
and infant mortality (Spears, 2012a), child height (ibid.), cognitive achievement (Spears
and Lamba, 2015), and adult wages (Lawson and Spears, 2016). In the vein of the analysis
we conduct in this paper, Headey (2015) applies econometric methods to Demographic and
Health Surveys in Ethiopia to identify an effect of improved sanitation on child height,
and Spears (2013) investigates the difference in child height between India and Africa and
documents that cross-country variation in sanitation can statistically explain a large
fraction of international height differences. Several studies of sanitation programs,
however, document no health impacts. Clasen et al. (2014), for instance, find no
significant health impact in an RCT studying a government sanitation program in Orissa.
Patil et al. (2014) similarly find no impact in a sanitation study conducted in Madhya
Pradesh. The authors of both studies note, though, that the absence of an impact on health
may have been because latrine use remained low despite large increases in latrine
coverage.3

<hs>  Sanitation in Cambodia</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

Cambodia is a Southeast Asian country of 14 million people. Three-fourths of the
population – and 90% of Cambodia’s poor – live in rural areas (Sobrado et al., 2014). The
country has a moderate population density of about 75 people per square kilometer. Over
the five-year period we study from 2005 to 2010 the fraction of the population living on
less than $1.25 a day fell from around 35% to under 20%, and GDP per capita, in purchasing
power parity terms, increased from $1962 to $2513 (2011 dollars), according to World Bank
World Development Indicator Statistics. Open defecation has historically been high in
Cambodia. We study the change over the period from 2005 to 2010, when exposure to open
defecation of the average child under five fell by about 14 percentage points from 74% of
the average child’s community in 2005. Sanitation coverage also varies substantially
across geographic areas within Cambodia (Robinson, 2007), another dimension of
heterogeneity that this paper exploits. Unsurprisingly, given Cambodia’s high rates of
open defecation relative to Southeast Asia, government, NGOs, and other partners have
played an important role in development activity in Cambodia. In the period in which we
study, a number of sanitation programs were active in Cambodia, mostly following a supply-
driven approach to sanitation. The private sector in Cambodia has played a significant
role in the provision of the majority of latrines, accounting for almost 80% of all
latrines built in the country (Rosenboom et al., 2011). Although there has been some
diversity of approach and method across programs and over time during this period, much of
the improvement in sanitation that this paper studies reflects new latrines that were
largely financed by households themselves, complemented by some subsidized provision
through development programs.

<h>EMPIRICAL STRATEGY</h>
------------------

Demographic and Health Surveys (DHS) are large, nationally representative surveys
conducted in poor and middle-income countries. We use data on the heights of children
under five years old in the two most recent DHS in Cambodia, conducted in 2005 and 2010.
Our dependent variable of interest is child height-for-age, which is a z-score of a
child’s distance in standard deviations from the average height of healthy children in a
reference population of the same sex and age in months. We compute z-scores using the
WHO’s 2006 international reference population, and follow their recommendation of omitting
children beyond six standard deviations from the mean. Our key independent variable is
local area open defecation. Each household is classified as defecating in the open or not
according to its report of where members “usually” defecate in the DHS questionnaire.4
However, infectious diseases often involve negative externalities (Gersovitz and Hammer,
2004), and intestinal disease resulting from open defecation is no exception: children are
exposed to fecal pathogens from neighboring households. Therefore, we compute the fraction
of households in a child’s survey Primary Sampling Unit (PSU) who defecate in the open, a
continuous variable from zero to one, as a measure of “local area open defecation.”5
Because all households potentially contribute feces to the environment but not all
households have children under five years old, we compute PSU averages from the DHS
household recode. All other variables are also taken from the DHS, except measures of
province mean consumption, which are from Knowles (2012), and population density, which
are computed from Cambodian census data. A concern in observational studies such as these
is that sanitation improvements may have been endogenously correlated with other
improvements, for instance in consumption or wealth. For this reason, we focus on
conducting an exercise in statistical accounting which provides an estimate of the
fraction of the change in child height that can be statistically accounted for by the
simultaneous change in exposure to open defecation. We thus do not attempt to estimate a
causal effect of open defecation on child height, but provide regression estimates as
supporting evidence of a relationship between open defecation and child height. In order
to minimize the concern that our regression results may be driven by other factors that
were simultaneously improving across Cambodia during the period of study, we employ
several different strategies. First, we use geographic fixed effects. Each province is
split into two parts classified as urban and rural. Urban and rural province part fixed
effects, henceforth called region fixed effects, control for factors that differ across
geographic areas that are correlated both with sanitation and child height. For instance,
international organizations have targeted development programs in certain provinces in
Cambodia. These programs may have led to sanitation improvements, but also could have
improved other services or infrastructures that influence child nutrition. Region fixed
effects control for such variation between regions. We also use time fixed effects to
control for secular changes in child height over time. Second, it may be the case that
open defecation in the child’s locality is correlated with other PSU-level variables such
as village infrastructure or wealth. Thus, for comparison as placebo independent variables
and as controls, we compute the fraction of households in a PSU with electricity, radio,
television, refrigerator, bicycle, motorcycle, and car, as alternative measures of local
living standards and infrastructure development. Third, we use a very extensive set of
household controls that address maternal nutrition, household socioeconomic status,
household education, and access to health care. These are discussed in more detail in
Section 2.1.

<hs>  Fixed effects identification strategy</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The dependent variable, z, is a child’s height-for-age z-score. Local area open defecation
is a fraction zero to one, and household open defecation is a binary indicator. Mother’s
height, BMI, and age at birth, are included to control for heterogeneity in maternal
nutrition, and to account for any possible direct effect of mother’s size (Ounsted et al.,
1986). Standard errors are clustered by survey PSU, the level of heterogeneity in the
independent variable of interest; 610 are more than enough for asymptotic clustered
standard errors (Cameron et al., 2008). The fixed effects identification strategy
differences out any fixed heterogeneity across regions within Cambodia, as well as the
secular trend in child height. We include eight further sets of control variables in
stages, in order to demonstrate robustness of our regression specification and the
stability of the estimates of interest: Bilpt Birth characteristics: 13 indicators for
birth order, 11 indicators for month of birth (Doblhammer and Vaupel, 2001), and whether
the birth occurred in an institutional facility. Ppt Province characteristics: Province-
level measures of average consumption and population density for 2005 and 2010. PSUlpt PSU
characteristics: Fraction, from zero to one, of households within the PSU with
electricity, radio, television, refrigerator, bicycle, motorcycle, and car.7 These
controls serve as both placebo independent variables and as alternative controls for PSU
welfare and infrastructure. Hilpt Household characteristics: seven binary indicators for
whether the household has electricity, and owns a radio, television, refrigerator,
bicycle, motorcycle, or car; ten indicators for floor material; 18 indicators for
household size, ten indicators for type of cooking fuel; and 14 indicators for water
source during the dry season and wet season, separately. These variables serve as
additional controls for household wealth and socio-economic status. Eilpt Education: the
number of years of education completed by the father and a binary indicator for mother’s
literacy. Vilpt Vaccinations: an indicator for the child having a health and vaccination
card, and eight binary indicators for the child receiving three rounds of the polio
vaccine, three Diphtheria, Pertussis, and Tetanus (DPT) shots, and Bacillus
Calmette–Guérin (BCG) and measles vaccines. Filpt Breastfeeding: a binary indicator for
the child being breastfed immediately. Milpt Milk consumption: a binary indicator for the
child being fed tinned, powdered, or fresh milk (de Beer, 2012; Baten, 2009; Baten and
Blum, 2014) the previous day and/or night. This variable is only available for the
youngest child under five.8 All specifications include 120 age-in-months times sex dummies
Ailpt to non-parametrically control for the correlation between height-for-age z-score and
age at measurement (Cummins, 2013). We test the mechanisms through which we believe open
defecation causes stunting using two methods. If the biological mechanisms we assume are
indeed occurring, we would expect the negative impact of open defecation on child height
to be greater in areas where people live nearer together and are thus more exposed to
others’ fecal pathogens. We test this mechanism using our data by introducing an
interaction between our open defecation variable and an indicator for whether the PSU is
urban. We would also expect there to be an association between open defecation and weight-
for-age if open defecation affects child nutrition by causing intestinal disease, and we
test for this as well. Finally, we perform two robustness checks. We use region by time
fixed effects in order to control for time-variant regional characteristics. While this
paper is primarily interested in exploring the extent to which changes in open defecation
can account for changes in height over time in Cambodia, this robustness check
nevertheless rules out any coincidental differences between regions over time from driving
our main result. We also include data from the 2000 DHS conducted in Cambodia. Cambodia
experienced a more modest decline in open defecation between 2000 and 2005 as compared to
the subsequent five years. However, inclusion of data from 2000 presents an opportunity to
check whether the main results of the analysis hold.

<hs>  Decomposition of change between 2005 and 2010</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

If open defecation is associated with child stunting, and if open defecation became less
common between 2005 and 2010, then how much of the increase in child height over this
period can be statistically accounted for by the reduction in open defecation? In a
separate analysis from the fixed effects estimates of the association between open
defecation and child height, we approach this question with three complementary
decomposition methods in Section 5. First, in the course of the regression analysis, we
see that controlling for local open defecation eliminates the statistical importance of
the indicator for survey year. Comparing this estimate to the actual change in child
height between 2005 and 2010 gives the fraction accounted for by the change in open
defecation. A final, most flexible, decomposition is non-parametric reweighting (DiNardo
et al., 1996).9 We generate a counterfactual estimate of 2005 child height by reweighting
children in 2005 to match the 2010 distribution of open defecation exposure. Comparing
this counterfactual estimate of the height of children in 2005 to actual child height in
2010 provides another estimate of the fraction of the difference in child height that can
be accounted for by the difference in open defecation. This function allows us to change
the distribution of exposure to open defecation for 2005 children so that it matches the
distribution for 2010 children.

<h>SUMMARY STATISTICS</h>
------------------

Children in our sample are on average almost two standard deviations shorter than the
healthy international reference population, and they live in poor households with parents
that have low levels of education. Table 1 presents sample means of many of the variables
used in our analysis. Note that these summary statistics, like all estimates in this
paper, are representative of children under five, and not of all Cambodians. The first and
second columns show averages for 2005 and 2010, and the third column reports a test that
these are different. Over the period we study, the height of children under five
significantly increased relative to the international reference population while the
fraction of open defecation in the average child’s community, and by individual
households, significantly decreased. Standards of living also detectably improved in
Cambodia between 2005 and 2010: households got richer, levels of education rose, and
institutional deliveries and early initiation of breastfeeding increased.

<hs>  Height is associated with open defecation: non-parametric descriptive regressions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Fig. 1 presents local polynomial regressions that document that child height is associated
with open defecation. Panel (a) plots child height as a function of age in months,
replicating the well-known fact that most stunting occurs in the first two years of life,
with height-for-age generally flat thereafter. These curves are plotted separately for
children who live in local areas (PSUs) where no one surveyed defecates in the open (seven
percent of children), where everyone surveyed defecates in the open (18% of children), and
the rest, living in areas with an intermediate sanitation profile. Children in all three
groups start off too short at birth, but the lines separate as stunting unfolds over the
first two years. Children exposed to the most open defecation are more than a standard
deviation shorter than children exposed to no open defecation, on average. However, open
defecation is not the only cause of child growth defects: even children exposed to no open
defecation are more than a standard deviation shorter than the reference population. One
reason why children exposed to better sanitation are taller is because they are also
richer. They are more likely to live in households that have toilets, while poorer
households are more likely to defecate in the open. However, open defecation imposes
negative externalities on everyone in the vicinity, and fecal pathogens in the environment
transmit disease to neighboring children. Panel (b) of Fig. 1 plots average child height-
for-age of children under five as a function of local area (PSU) open defecation.
Households that do and do not defecate in the open are plotted separately. Unsurprisingly,
children who live in households that use toilets are taller, on average, than children who
do not. However, the key feature of the graph is that both lines slant downwards. Whether
or not a child’s own household defecates in the open, she is shorter, on average, if more
of the households in her community do. What is the association between sanitation and
child height over time in Cambodia? Are the geographic areas that experienced a decrease
in open defecation the same areas that experienced an increase in child height? Panel (a)
of Fig. 2 visually explores this question. Each line in the figure connects one region’s
2005 averages of child height and rate of open defecation in the child’s locality to its
2010 averages. Each region represents an urban or rural part of a Cambodian province. Of
the 38 lines, 25 slope downwards, indicating that in 25 regions of Cambodia, average open
defecation in a child’s locality reduced and average child height increased. As a
preliminary non-parametric statistical significance test, a binomial distribution reports
that there is only a four percent chance of seeing at least 25 of 38 lines slope downwards
if these slopes are independent of one another and equally as likely to slope up or down,
indicating no association at all. The main contribution of this paper is to explore what
can account for the increase in child height in Cambodia between 2005 and 2010. Panel (b)
of Fig. 2 presents a visual depiction of the extent to which the change in open defecation
can account for the change in child height. Within the two years 2005 and 2010, local
polynomial regression lines plot average child height-for-age against open defecation
rates in the locality. The lines are relatively close to one another and quite nearly pass
through both of the overall year average points. Note that this is not mechanically
determined: although each year’s average point must be on or near its own line, the two
lines could be vertically far apart. If the lines were vertically separated, this would
indicate differences in average child height for the two years even at the same level of
open defecation in the locality. However, the fact that the lines are close together
indicates that the association between height and sanitation in 2005 is similar to the
association in 2010. Since the points are on similar lines, it appears that the within-
year association between height and sanitation can statistically account for the between-
years change in height. This figure is a visual representation of the results of our
decomposition techniques, which we will discuss in further detail in Section 5 of this
paper. Before we do so, however, we will first explore the relationship between exposure
to open defecation and child height in greater detail using regression analysis.

<h>CHANGES WITHIN PROVINCES: REGRESSION EVIDENCE</h>
---------------------------------------------

This section explores whether the regions that experienced a greater decrease in open
defecation also experienced a greater increase in child height between 2005 and 2010.
Table 2 reports our regression results. Panel (a) shows estimates from OLS regressions
without fixed effects, while Panel (b) displays results from regressions with region fixed
effects. The OLS regressions identify the variation both between and within regions, while
the fixed effects regressions isolate the variation occurring within regions, indicating
that the relationship is not driven by coincidental differences between regions. An
increase from zero to one in the rate of open defecation in the child’s locality is
linearly associated with a decrease in children’s height by between 0.3 and 0.5 standard
deviations, using fixed effects and varying sets of control variables.

<hs>  Regression results</hs>
  ~~~~~~~~~~~~~~~~~~

Column 1 simply reports the average improvement in child height from 2005 to 2010. Could
the reduction in open defecation account for this overall increase in child height?
Notably, when we introduce open defecation in the child’s locality in Column 2, the 2010
dummy variable becomes statistically and practically insignificant, indicating that the
change in sanitation can statistically explain the average change in height over time. As
we progress from Column 3 to Column 6, we progressively add more control variables. Column
3 adds household open defecation, mother’s anthropometry and age at birth, birth order,
month of birth, and whether the birth occurred in a facility.10 While measures of maternal
anthropometry are unsurprisingly predictive of child height, they do not diminish the role
of sanitation. In Column 4, we further add province-level consumption and density, and PSU
averages for electricity coverage and radio, television, refrigerator, bicycle,
motorcycle, and car ownership. Inclusion of these variables helps control for PSU-level
infrastructure and wealth. Column 5 adds controls for household wealth and socio-economic
status by including household-level indicators for ownership of the assets listed above,
floor material, household size, type of cooking fuel, water source, father’s educational
attainment, and mother’s literacy. It also includes vaccination data for polio, DPT, BCG,
and measles, availability of an immunization card, and early initiation of breastfeeding.
In Column 6, an indicator for milk consumption is included. This model has fewer
observations because this variable is only available for the youngest child under five,
rather than for all children under five. For this reason, Column 5 represents the authors’
preferred specification. All specifications include 120 age-in-month dummies, separately
for boys and girls.11,12,13,14 Three conclusions emerge from the table. The first is the
robustness of the coefficient on open defecation in the child’s locality. The variable
remains highly statistically significant in all specifications. If instead of clustering
standard errors at the PSU level, we cluster at the more conservative level of 38 regions,
the t-statistic on open defecation in the child’s locality in the most controlled
specification, Column 5 of Panel (b), becomes −2.75, although this may be too few clusters
for asymptotic results (Cameron et al., 2008). Secondly, the clear similarity in the size
of coefficients from the OLS and fixed effects regressions suggests that the results from
the OLS regressions are not a spurious artifact of heterogeneity across regions. Fixed
effects are well-known to risk attenuation bias. However, that appears to be unlikely in
this case due to the small differences between corresponding models of Panel (a) and Panel
(b).15 Finally, an important result for policy is that the coefficient on household open
defecation is not statistically significant.16 This is unsurprising because open
defecation, like other sources of infectious disease, involves important negative
externalities. In Table 3, we split the sample by whether or not the household in which
the child lives defecates in the open. Open defecation in the community predicts child
height, regardless of whether the household defecates in the open. This result
corroborates the importance of negative externalities (Geruso and Spears, 2015). Because
such externalities are a classic economic rationale for public action, they point to the
importance of a policy response to open defecation.

<hs>  Mechanism check: steeper slope in urban areas</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The importance of open defecation in the child’s locality, rather than the household’s own
open defecation, indicates a key role for externalities of disease. If so, then because
children are more exposed to others’ fecal pathogens where people live nearer together, we
would further expect that open defecation should have a steeper association with child
height in urban areas, where population density is particularly high (Hathi et al., 2014;
Bateman et al., 1993; Bateman and Smith, 1991). We test this by introducing an interaction
between prevalence of open defecation in the locality and an urban dummy to the
specification in Column 2 of Table 2. Does open defecation indeed have a steeper
association with child height in urban parts of Cambodia than in rural parts? The fraction
of open defecation in the PSU interacts with an indicator for urban place, with and
without fixed effects. An increase in the rate of open defecation in the child’s locality
from zero to one is associated with a 0.34 (s.e. 0.16) standard deviation greater decrease
in average child height in urban areas compared to rural areas using a standard OLS model,
and a 0.41 (s.e. 0.22) standard deviations greater decrease using a model with region
fixed effects. These coefficients are statistically significant at the two-sided ten
percent level. This finding is consistent with Spears (2012a), Spears (2013), and Hathi et
al. (2014).

<hs>  Mechanism check: weight-for-age</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

If open defecation does indeed affect child height by causing intestinal diseases that
lead to undernutrition, then we may simultaneously expect to see an effect of open
defecation on weight, another measure of nutritional status. Weight-for-age is associated
with recent diarrheal episodes (Schmidt et al., 2010) and environmental enteropathy (Lin
et al., 2013; Humphrey, 2009). As a measure of nutrition, weight-for-age is more
responsive to recent changes in diet, care practices, or the disease environment, while
height-for-age is a measure of net nutrition in the first two years of life (Waterlow
1972; Black et al., 2008). Open defecation in the child’s locality statistically
significantly predicts weight-for-age, with and without fixed effects. Replacing height-
for-age with weight-for-age in Column 3 of Table 2 shows that an increase in open
defecation in the child’s locality from zero to one is associated with a reduction in
weight of 0.56 (s.e. 0.083) standard deviations in a standard OLS model, and 0.23 (s.e.
0.074) standard deviations in a model with region fixed effects. These coefficients are
significant at the two-sided one percent level.

<hs>  Robustness checks</hs>
  ~~~~~~~~~~~~~~~~~

We test the robustness of our results using two methods: including region by time fixed
effects in order to isolate the variation occurring within regions in a particular year,
and adding data from the DHS conducted in Cambodia in 2000. Table 4 reports the results of
our robustness checks. In Column 1, we include region by time fixed effects. This more
restrictive specification changes the coefficient on open defecation in the child’s
locality only very slightly: using the same set of controls as in Column 5 in Table 2, the
associated reduction in child height arising from an increase in open defecation in the
child’s locality from zero to one is 0.35 standard deviations using region fixed effects
(Table 4, Column 1) and 0.29 using region by time fixed effects (Table 4, Column 2).
Column 3 of Table 4 includes data from the 2000 Cambodian DHS. Between 2000 and 2005,
Cambodia experienced a much more modest decline in open defecation of only eight
percentage points, compared to the subsequent five years in which the decline was 14
percentage points. Nevertheless, including data from the year 2000 only supports our main
result.

<h>DECOMPOSITION OF THE 2005–2010 INCREASE IN CHILD HEIGHT</h>
-------------------------------------------------------

How much of the increase in child height between 2005 and 2010 can be explained by the
decrease in average exposure to open defecation? Econometric decompositions ask how much
of the difference in the outcome variable across two groups can be accounted for by
observable differences in input variables (Fortin et al., 2011). Although the canonical
use of decompositions in labor economics is to analyze differences in economic outcomes
(such as wages) between two groups (such as black and white people in the United States),
here we will be asking how much of the difference in child height in Cambodia between 2005
and 2010 can be accounted for by the difference in the level of open defecation in a
child’s locality. In general, econometric decompositions of observational data are tools
of statistical accounting that may or may not have a causal interpretation depending on
the details of the data and the source of heterogeneity studied. We thus interpret
decomposition results conservatively as accounting for differences. In Section 3.1, we
discussed Panel (b) of Fig. 2, which presents a visual depiction of the extent to which
the change in open defecation can explain the change in child height. Each line plots
local polynomial regressions of the sanitation height gradient for each year. The relative
closeness of the lines indicates that the gradient is similar in both years, and the fact
that the overall year averages for both years are almost on these lines indicates that the
within-year association between height and sanitation appears to statistically account for
the between-years change in height. Various methods of econometric decomposition are
available, and we study three. The first and simplest was already presented in the
difference between Columns 1 and 2 of Table 2. Adding a linear control for open defecation
in a child’s locality (PSU mean open defecation) eliminates a statistically significant
difference in child height between the two DHS rounds. Using OLS and fixed effects
estimation strategies, controlling for open defecation in the child’s locality
statistically accounts for 88% and 86% of the difference in child height from 2005 to
2010, respectively (see Table 5). The following two sub-sections will consider a Blinder
(1973) – Oaxaca (1973) decomposition, and will apply a non-parametric reweighting
technique.

<hs>  Blinder-Oaxaca decomposition</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Blinder-Oaxaca decomposition calculates the explained change in child height between 2005
and 2010 using an estimate of the height-sanitation gradient. In this case, two
regressions separately estimate β12005 and β12010 and then average them to create a
counterfactual within-year height sanitation slope. Multiplying this by the difference in
the average exposure to open defecation between 2005 and 2010 provides an estimate of the
change in child height that can be accounted for by the change in open defecation. As
Table 5 shows, this approach finds that the reduction in open defecation to which the
average child was exposed can statistically account for 0.12 of the 0.13 standard
deviation difference in child height. Thus, 92% of the difference in height can be
accounted for by the difference in sanitation.

<hs>  Non-parametric reweighting decomposition</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

This method creates a counterfactual average height for children in 2005, reweighted to
match the 2010 distribution of open defecation. In particular, the sample is split into 12
bins of PSU open defecation levels: ten deciles with extra categories for open defecation
of zero and open defecation of one. These are crossed with an indicator for own household
open defecation to create 22 overall open defecation bins (there are 22 instead of 24
because there are no children in households that openly defecate who also live in PSUs
where nobody sampled defecates in the open, and vice versa). Then, within each of the 22
bins, the total sample weight is computed separately for 2010 and 2005. A new set of
weights is computed for children in 2005 by multiplying their sampling weight by the ratio
of their bin’s 2010 total sampling weight to their bin’s 2005 total sampling weight.
Finally, the new weighted average represents the counterfactual height of children in 2005
if they had been exposed to the same levels of open defecation as children in 2010. This
result is compared with the other decomposition methods in Table 5. The true sample mean
height for age was −1.77 in 2005 and −1.64 in 2010. When the 2005 sample is reweighted to
match the 2010 sanitation distribution, the counterfactual mean height-for-age is −1.63,
essentially the same as the true 2010 average (the difference is not statistically
significant, t = 0.29). Therefore, all three approaches to decomposing the change over
time in child height reach similar conclusions. Using simple pooled regression, a Blinder-
Oaxaca decomposition, or non-parametric reweighting, the decline in exposure to open
defecation can statistically account for almost all of the approximately 0.13 standard
deviation increase in height-for-age.

<h>CONCLUSION</h>
----------

Child height is an important economic variable predicting adult human capital, cognitive
achievement, and health. The average child under five in Cambodia was 0.13 standard
deviations taller in 2010 than in 2005. Decomposition analysis finds that much of the
increase in child height between 2005 and 2010 can be accounted for by the simultaneous
reduction in open defecation. At the same time, regression analysis finds a robust and
large association between exposure to open defecation and child height. The point
estimates computed in this analysis are consistent with other studies. A meta-analysis
combining data from three large-scale randomized interventions conducted independently in
India, Indonesia, and Mali finds that eliminating open defecation in a village in which
everyone practices open defecation is associated with a 0.4 standard deviation increase in
height (Gertler et al., 2015). This is similar to the point estimates found in this paper
of between 0.3 and 0.5 standard deviations, with region fixed effects and controls. The
change in child height over this period of time represents an important difference:
Spears’ (2012b) estimates of the height-cognitive achievement gradient for Indian children
suggest that a 0.13 standard deviation increase in child height would be associated with a
1–4 percentage point increase in the probability of being able to read words or paragraphs
among 8–11 year-olds. This difference is also quantitatively similar to the India-Africa
height gap (Spears, 2013). These results indicate that widespread open defecation could be
a critical constraint for human development. Moreover, we have seen various indicators of
the role of negative externalities in propagating fecal pathogens. The health benefits of
better sanitation are significant, and in Cambodia, the cost associated with constructing
a latrine can be as low as $25 (Rosenboom et al., 2011). Lawson and Spears (2016) find a
robust relationship between adult wages and the disease environment during childhood in
India, and the fiscal implications indicate that public investment in sanitation
infrastructure may come at very low net present cost. Interventions that are long-term are
more likely to lead to sustainable improvements in nutritional indicators for children
(Reiger and Wagner, 2015). Thus, if latrine adoption is durable, it can have a substantial
impact on child height. Between 2005 and 2010, open defecation decreased, and child height
increased, but open defecation is still common in Cambodia and the mean child was still
1.64 standard deviations below the healthy reference population in 2010. In any country
where this is the case, spillovers of poor sanitation indicate that reducing open
defecation must be a policy priority.


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<ART>Do emission subsidies reduce emission? In the context of environmental R&D organization
================================================================================

Authors: Yasunori Ouchida, Daisaku Goto
DOI: 10.1016/j.econmod.2013.10.009
Year: 2014  |  Pages: 511-516
ASJC codes: 2002
Keywords: Cournot duopoly, Emission reduction, Emission subsidy, Emission tax, Environmental R&D

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper, which reexamines the Poyago-Theotoky model, provides additional investigation that was conducted under a corrected environmental damage parameter. As new findings, we obtain the following. First, social welfare under a time-consistent emission tax (emission subsidy) policy is always welfare-enhancing rather than the case of laissez-faire. Second, if the environmental damage parameter is sufficiently small, then the equilibrium emission tax rate is invariably negative. It is therefore an emission subsidy. Moreover, total emissions under the emission subsidy scenario become less than those under laissez-faire if the damage parameter is sufficiently small, and if the R&D cost is low. However, total emissions under the emission subsidy become greater than those under laissez-faire if the damage parameter is sufficiently small, and if the R&D cost is high. © 2013 The Authors.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

In an industrialized economy in which giant firms dominate markets, perpetual innovation
drives the rate of growth in living standards continuously. Particularly, it is true that
the petroleum and chemical industries have both been oligopolistic, routinizing corporate
and environmental innovations, and contributing to economic growth with some environmental
friendliness. These industries typically have developed pollution abatement instruments
such as desulfurization equipment and denitrification equipment, which are categorized
into end-of-pipe technologies. Emission regulation has received great amounts of attention
from many researchers. Studies of environmental regulation and emission-reducing R&D in an
oligopolistic market have been conducted by Chiou and Hu (2001), Puller (2006), Riveiro
(2008), Celik and Orbay (2011), Yakita and Yamauchi (2011), Pal (2012), and others.
Particularly, Jaffe et al. (2002) and Requate (2005) provide excellent surveys in that
field. The strategic behavior of polluting oligopolists has a strong impact on social
welfare. Therefore, it is highly necessary for policy designers to accumulate the welfare
performances and implications of various environmental policy instruments in oligopolistic
markets. In environmental policy studies, the timing of policy variables is an important
topic. Poyago-Theotoky (2007) presents pioneering work on emission tax policy and
competition policy related to quantity-setting duopolists with end-of-pipe technology.
Particularly, that investigation examines whether polluting Cournot duopolists'
coordination of behavior in environmental R&D is socially allowable or not when the
government has no precommitment capability with respect to emission taxes. The study finds
important policy implications for socially desirable R&D formation under time-consistent
emission taxes. Furthermore, Poyago-Theotoky (2010) announces a corrigendum showing that
the negative emission tax (i.e., emission subsidy) might be partially justified if it
considerably improves the market inefficiency caused by Cournot duopolists. Indeed, this
is a surprising result, but the fundamental question remains. That is “When does an
emission subsidy reduce (or increase) emissions?” The answer is fervently sought by policy
designers. Nevertheless, little attention has been devoted to that question. In real
society, many developed countries confront obligations related to greenhouse gas
reduction, along with international commitments such as the Kyoto Protocol. In addition,
most emerging countries seek both industrialization and environmental improvement.
Therefore, it is necessary for social planners to investigate the regulatory circumstances
under which a time-consistent emission subsidy reduces (or increases) emissions. On the
other hand, in the existing literature on environmental regulation, negative emission
taxes (emission subsidy) in oligopolistic markets are discussed by Requate (1993a, 1993b),
Petrakis and Xepapadeas (1999, 2003), David (2005), Fujiwara (2009), Ben Youssef and Dinar
(2011), and others.1 Those studies point out that negative emission tax rate can exist in
equilibrium when environmental damage is sufficiently small. However, investigations of
negative emission taxes are utterly inadequate. This paper carefully analyzes the
emission-reducing effects of negative emission taxes. Arguments presented in this paper
proceed as follows. Section 2 introduces the Poyago-Theotoky (2007) model and equilibrium
outcomes. Section 3 presents an examination of the sign of the equilibrium emission tax
rate and effects on total emissions. Section 4 presents policy implications and
conclusions.

<h>MODEL AND EQUILIBRIUM OUTCOMES</h>
------------------------------

This section presents the model and its equilibrium outcomes.

     <hss>Market structure</hss>

        Considering an industry comprising two homogeneous firms, firm i and firm j,
        engaging in quantity competition with the same cost structure and emissions-
        reducing technology, qi is assumed to denote firm i's output. Inverse demand is
        given as p(qi,qj) = a − (qi + qj), (i, j = 1, 2; i ≠ j), where a(> 0) is a market
        size parameter.

     <hss>Environmental R&D and cost structure</hss>

        The value of each firm's emissions per unit output is assumed to be one. Firm i's
        environmental R&D effort is denoted as zi. Both firms use end-of-pipe technology
        for pollution abatement. Although this abatement technology is insufficient to
        reduce emissions per unit output, it mitigates emissions by adsorbing emissions at
        the end of the production process. Firm i receives benefits not only from its own
        environmental R&D efforts but also from the efforts of its rival. When firm i's
        production level is qi, then the R&D expenditures (γ/2)zi2, (γ > 0) enable firm i
        to abate its emissions from qi to ei(qi,zi) ≡ qi − zi − βzj.2 A lower value of γ
        implies higher efficiency of the environmental R&D cost. Symmetric parameter β ∈
        [0,1] denotes the spillover effects of R&D. Firm i's positive externality from
        rival's R&D efforts is denoted as βzj. No fixed costs for pollution abatement are
        necessary. In addition, firm i's total cost function is additively separable with
        respect to production costs and R&D expenditures: C(qi,zi) = cqi + (γ/2)zi2, (c >
        0, A ≡ a − c > 0).

     <hss>Timing</hss>

        The regulator has no precommitment ability for emission tax rate t. The time
        structure is the following: Stage 1: Firm i determines zi to maximize its own
        profit (πi) or joint profits (πi + πj). Stage 2: The regulator determines emission
        tax rate (t) to maximize social welfare. Stage 3: Firm i determines output level
        (qi) noncooperatively to maximize its own profit.

<hs>  Equilibrium outcomes</hs>
  ~~~~~~~~~~~~~~~~~~~~

Poyago-Theotoky (2007) examines two environmental R&D scenarios (R&D competition and R&D
cartelization) and derives the subgame-perfect Nash equilibrium (SPNE) under a time-
consistent emission tax.4 To begin, we explore the case of environmental R&D competition.
In stage 3, firm i's profit is πi(qi,qj) = {a − (qi + qj)}qi − cqi − t{qi − zi − βzj} −
(γ/2)zi2. Each firm chooses an output level noncooperatively and simultaneously to
maximize its own profit. From the first-order conditions, the symmetric equilibrium output
is calculated as q(t) = (A − t)/3. In the first stage, firm i's profit is πi(zi,zj) =
[q(t(zi,zj))]2 + t(zi,zj){zi + βzj} − (γ/2)zi2. Each firm determines its environmental R&D
efforts noncooperatively and simultaneously. From the first-order conditions
∂πi(zi,zj)/∂zi = 0, (i, j = 1, 2; i ≠ j), we obtain the equilibrium R&D efforts zN and the
equilibrium values of other variables. The results are presented in Table 1.5
Environmental R&D cartelization implies that each firm determines its environmental R&D
effort collusively to maximize joint profits (πi(zi,zj) + πj(zi,zj)) during the first
stage. Each equilibrium value under R&D cartelization is also reported in Table 1.

<h>INVESTIGATIONS AND RESULTS</h>
--------------------------

This section presents examination of the sign of the equilibrium emission tax rate and
effects on total emissions.

<hs>  Sign of emission tax rate</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~

Poyago-Theotoky (2007) proves that each firm always has some incentive for R&D
cooperation, that is πC ≥ πN, and that SWC > SWN if 1/2 < d < 3/2.6 Furthermore, that
research shows that social welfare under environmental R&D cartelization is higher than
the case of noncooperative environmental R&D, except in the case of large damage and lower
R&D cost. The exceptional case is presented as Region IV in Fig. 1. In Region IV, SWC <
SWN. On the other hand, in Regions I, II, and III in Fig. 1, SWC > SWN. Precisely
speaking, if d ≥ 3/2, then SWC ≥ (<) SWN for all γ ≥ (<)γφ.7 In this model, a negative
emission tax rate (i.e., emission subsidy) is fundamentally equivalent to the policy mix
of a production subsidy and an abatement tax because each firm's emission function is
assumed as pollution generated by production minus net abatements. A production subsidy
has two effects. One is a damage-increasing effect. The other is the decreasing effect of
market inefficiency. When d is sufficiently small, the increasing effect of environmental
damage is dominated by the improvement effect on market inefficiency. This is the economic
intuition underlying the negative emission tax rate.10 Particularly, part (i) of
Proposition 1 is newly obtained under the parameter range corrected by Ouchida and Goto
(2011), whereas Poyago-Theotoky (2010) points out the existence of a negative emission tax
in the case of part (ii) of Proposition 1. As shown by Requate (1993a, 1993b), Petrakis
and Xepapadeas (1999, 2003), Fujiwara (2009), Ben Youssef and Dinar (2011), and others, a
negative emission tax can be justified socially when environmental damage is sufficiently
slight.11 The Poyago-Theotoky (2007) model is related with these studies, and is also
somewhat different in the following four points: timing of emission taxation, market
structure, spillover effect, and the type of emission function. Despite such differences,
Proposition 1 of the present paper and Poyago-Theotoky (2010) show that a negative
emission tax is realized in equilibrium when environmental damage is sufficiently small.
This fact suggests that the necessary condition for negative emission tax is still robust
in the case of a time-consistent emission tax policy toward Cournot duopolists.

<hs>  Negative emission tax and total emissions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Readily inferred from Proposition 2 (iv). □ In Fig. 1, γE is described as the borderline
between Region I and Region II. In both Regions I and II, the sign of the equilibrium
emission tax rate is negative: the emission subsidy is realized in the equilibrium.
Therefore, we can identify that in Region I, the emission subsidy yields greater total
emissions than those under laissez-faire. In Region II, however, it yields less total
emissions than those under laissez-faire, i.e., the emission subsidy reduces total
emissions. Among reports of existing studies of the literature, except for this research,
no study has ever explicitly examined emission-reducing and emission-increasing effects
under emission subsidy. We now explore the intuition underlying the existence of Regions I
and II. As environmental damage d decreases, the equilibrium emission tax rate tC, R&D
effort zC, and accordingly R&D effort with a spillover effect (1 + β)zC respectively
denote decreases. Additionally, as the R&D cost parameter γ becomes large, each value of
zC and (1 + β)zC decreases greatly. Ultimately, if the value of d is sufficiently small,
then the sign of tC becomes negative. However, as the value of d becomes small, the
equilibrium production level per firm qC becomes greater. Consequently, as shown by Region
I, total emissions under emission subsidies become greater than that under laissez-faire
if the damage parameter is sufficiently small, and if R&D cost is not low. In Region II,
although the sign of equilibrium emission tax rate is negative, total emissions under an
emission subsidy become smaller than the case of laissez-faire because the emission-
increasing effect is dominated by the large abatement effect.12 From the definitions of
γCt and γE in Eqs. (2) and (3), we obtain the following proposition with respect to Region
II. The greater the spillover effect becomes, the broader the regulatory circumstances in
which emission subsidies reduce total emissions. Proposition 3 states that Region II is
increasing in β. Fig. 1 presents this result graphically. The value of β can be regarded
as the level of intellectual property rights (IPR) protection. Therefore, a stronger IPR
protection level generates smaller Region II. When the spillover is perfect (β = 1),
Region I becomes the smallest.

<h>POLICY IMPLICATIONS AND CONCLUDING REMARKS</h>
------------------------------------------

In this section, we derive two policy implications from our analysis explained above: one
is derived from part (i) of Proposition 2 (i.e., Region I in Fig. 1); the other is derived
from part (ii) of Proposition 2 (i.e., Region II). The latter is more meaningful. The
petroleum refining industry and the petrochemical industry are examples of polluting
industries using desulfurization equipment and denitrification equipment. Those
industries, which are directly applicable to this model, emit plenty of greenhouse gasses.
This study provides fundamental results that are expected to be useful in avoiding policy
failure when the regulator's policy variable is a time-consistent emission tax. Part (i)
of Proposition 2 implies that if the environmental damage parameter is sufficiently small,
and if R&D cost parameter is sufficiently high, then the government will choose a time-
consistent emission subsidy that yields “greater emissions” than those under laissez-faire
in Cournot duopoly. Now, let us assume that the government faces the obligation of
emission reduction. In this case, a policy contradiction is unavoidable. In reality,
governments of the developed countries committed to reduction of greenhouse gas emissions.
The regulator of those countries should investigate the real value of R&D spillover. On
the other hand, part (ii) of Proposition 2 implies that if the environmental damage
parameter is sufficiently small, then the government will choose a time-consistent
emission subsidy that yields “less emissions” than those under laissez-faire in Cournot
duopoly. That is to say, an emission subsidy can reduce the total emissions.13 Previous
studies have devoted little attention to such circumstances (i.e., Region II). As
described in this paper, our new findings present two points of particular significance.16
One is derivation of incremental policy implications. Another is to give a further
theoretical foundation for time-consistent emission tax policy in quantity-setting
duopoly. This research plays an indispensable complementary role for contributions by
Poyago-Theotoky (2007, 2010).


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<ART>Do fast food restaurants surrounding schools affect childhood obesity?
======================================================================

Authors: Jebaraj Asirvatham, Michael R. Thomsen, Rodolfo M. Nayga, Anthony Goudie
DOI: 10.1016/j.ehb.2019.01.011
Year: 2019  |  Pages: 124-133
ASJC codes: 2001
Keywords: Body mass index, Childhood obesity, Fast food, Instrumental variable estimation, School food environment

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

In this study, we estimate the effect of fast food environment surrounding schools on childhood body mass index (BMI). We use two methods that arrive at a similar conclusion, but with different implications. Using school distance from the nearest federal highway to instrument for restaurant location, we find the surrounding restaurants to only marginally affect a student's BMI measure. The effect size also decreases with increasing radial distances from school, 0.016 standard deviations at one-third of a mile and 0.0032 standard deviations at a mile radial distance. This indicates the decreasing influence of restaurants on a child's BMI as its distance from school increases. On a subset of students who were exogenously assigned to different school food environment, we find no effect of the fast food restaurants. An important contextual aspect is that nearly all schools in this sample observed closed campus policy, which does not allow students to leave campus during lunch hours.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Rising rates in childhood obesity have become an important worldwide health and public
policy issue. Even though this has received more attention in the United States, childhood
obesity is a growing problem in other countries, including those in Europe and Asia.
Because the majority of children attend public schools, there is much interest in
regulating the food environment in schools to promote health objectives (Story et al.,
2009; Sharma et al., 2009). France, for example, banned food promotion in schools, whereas
Mexico and India have banned sales of sodas and certain unhealthy foods in schools
(Villanueva, 2011; Barquera et al., 2013; Khandelwal and Reddy, 2013). In the US,
regulation has mostly focused on school meals and those foods stocked in school vending
machines1 . Addressing childhood obesity has become a policy priority, especially because
obesity during childhood may continue into adulthood (Serdula et al., 1993). Most public
policy efforts have focused on school lunches and other food products sold within the
school. There is a growing concern, however, that fast food restaurants around schools
might increase caloric intake among children and thereby increase obesity (Davis and
Carpenter, 2009). There are incentives for fast-food restaurants, especially national
chains, to target children for increasing current sales and creating brand loyalty. This
is more apparent among hamburger fast food restaurants, sandwich places, and pizzerias
(Austin et al., 2005). Collectively, we will refer to these three restaurant types as fast
food restaurants. An important question of public policy relevance is to know whether the
presence of fast food restaurants around schools have any effect on childhood obesity. We
seek to identify the effect of fast food restaurants surrounding schools on a child’s BMI.
Estimating the causal effect of fast food restaurants surrounding schools, however, is
challenging due to: a) self-selection of families into neighborhoods; b) omitted variable
bias; and c) selection of fast food restaurants in into neighborhoods according to fast-
food demand. Self-selection of parents due to occupation, education or other reasons could
create neighborhoods that could be similar in their attitude towards health and well-being
of their children. Omitted variables in the determination of a child’s BMI could include
features of the school food environment. We address biases in the estimation using an
instrumental variables approach, where the instrument is the proximity of the school to US
highways that create a demand for fast food restaurants to serve highway travelers. This
instrument has been used in several studies (for example, Dunn, 2010; Anderson and Matsa,
2011). In addition to this method, we estimate individual-level fixed effects for a subset
of students who were exogenously reassigned to another school. This strategy follows that
used by Asirvatham et al. (2018) in their analysis of peer effects. Both these methods
arrive at a similar conclusion – fast food restaurants surrounding schools have a
negligible effect on BMI outcomes of school children. The analytic sample is based on
measured BMI records from an ongoing BMI screening program within the Arkansas public
school system. There are several ways that fast food restaurants surrounding schools could
influence BMI outcomes. First, fast food restaurants and pizzerias offer calorie-dense
foods that play a direct role in obesity. Even though most schools in this study observe
closed campuses, a high density of restaurants around schools will generally increase the
likelihood that students visit restaurants before or after school hours either
unsupervised with friends or with a parent or caregiver. Second, restaurants located
nearby reduces travel cost to obtain food. It could also be that proximity disincentivizes
traveling longer distances to purchase healthier foods. Third, exposure to the sight of
restaurants might increase the likelihood that children would choose fast foods after
being exposed to fast food restaurants en route from school to home. Fast food signage
could reinforce marketing messages aimed at children and increase likelihood of fast food
requests on food-away-from-home meal occasions. School meals can be served as early as
10:30 am and many children will be hungry at the end of the school day. The presence of
fast foods in school environment could thus increase desire for fast foods on other dining
occasions regardless of whether the child consumes fast food on the way to or from school.
Finally, teachers who leave campus for lunch could bring in items from restaurants (e.g.,
drink cups) and thereby model fast food as a reasonable meal choice. This is similar to
the argument that advertisements targeting children might increase fast food consumption
(Jashinsky et al., 2017). Study participants in Cambridgeshire, UK, who faced a greater
exposure to fast food outlets showed higher intake of takeaway food (Burgoine et al.,
2014).

<h>CONTRIBUTION TO THE CURRENT LITERATURE ON FAST FOOD AND OBESITY</h>
---------------------------------------------------------------

Much of the work in this line of research provides some evidence of a positive association
or correlation of obesity rates or BMI with restaurant availability or proximity (Williams
et al., 2014). Most of the studies are correlational and therefore it is difficult to
imply any causality. In this section, we discuss few of the studies that have conducted a
more rigorous analysis going beyond correlation or association. These studies in general
find a small effect. Three studies used an instrumental variables strategy based on
proximity to highways (or highway on/off ramps), to estimate the impact of fast food
density on body weight outcomes among adults. In a county-level study, Dunn (2010) used
the number of exits on a highway within a county to instrument for the number of
restaurants in a county and finds restaurant availability to effect only females and non-
whites in medium-density counties in 11 states. Such a relationship was not found in rural
or low-density counties. In a similar study on residents of central Texas, Dunn et al.
(2012) reported only non-whites to exhibit higher obesity rates in response to fast food
exposure. These authors also used distance to the nearest major highway as an instrument
for the fast-food restaurant. Anderson and Matsa (2011) find no effect of fast food
restaurants. They also exploit the variation in travel costs of local residents to
restaurants along interstate highways, which primarily serves travelers. Using related
data, they observed that obese individuals complement eating outside by consuming
nutritionally deficient or “junk foods.” They conclude that policies focusing solely on
regulating fast food restaurants may not achieve any significant reduction in BMI. The
above studies examine adult populations. Two studies analyze fast food restaurants around
schools and find fast food restaurants to significantly affect childhood obesity rates.
Currie et al. (2010) uses a cross-sectional sample of students from grade 9 in public
schools in California. In their study, the effect is identified by comparing groups of
individuals at only slightly different distances to a restaurant (i.e., of only one-tenth
of a mile). They measure changes in exposure, with obesity being measured as the fraction
of obese students at the grade-level in a school. In their study, they use changes in
obesity prevalence in the same grade (grade 9) but across different years. Alviola et al.
(2014) study the public school sample in Arkansas. Following the earlier studies on adult
populations, their instrumental variable was the distance of school from the nearest
highway. Using school-level cross-sectional data, they report coefficients that measure
the difference in obesity rates across schools that face different restaurant counts.
Their study estimates a 1.23 percentage point increase in school obesity rates in response
to an additional restaurant within a one-mile radius from a school. In this article, we
also focus on Arkansas public schoolchildren. However, unlike Alviola et al.’s (2014)
school-level analysis, this study uses individual-level analysis of BMI z-scores over
time; i.e, we use student-level panel data in contrast to the school-level cross-sectional
data they used. In addition to an identification strategy based on an IV estimation using
distance of schools to the nearest highway as an instrument, we also employ an additional
identification strategy based on a plausibly exogenous reorganization of public schools
that caused some children to be reassigned to a new school zone. Hence, these re-assigned
students face a new food environment in their newly assigned school. The present article
extends these studies in several ways. One, we have a unique panel dataset, which gives us
the ability to measure changes within a student and estimate fixed effects at the
individual level. Several of the previous studies use obesity rates (proportion of obese
adults or children) or obesity status (a binary variable). We are able to estimate the
impact on precise changes in BMI in terms of standard deviations of the child’s BMI
z-score. Two, in contrast to several past studies, the BMI data used here are measured by
trained personnel, as opposed to being self-reported. Three, we control for the commercial
food environment near a child’s residence with precise geographic information. It is
important to control for other sources of calories because this could influence the
quality and quantity of food consumed. Four, as mentioned above, this study uses two
methods to identify the effect of fast food availability around schools on children’s BMI
z-scores: IV and the exogenous assignment of students to nearby schools as a result of a
court-mandated restructuring program. These are discussed in detail in the section
Identification Strategies.

<h>METHODS</h>
-------

The primary aim of this study is to estimate the effect of fast food restaurants
surrounding schools on childhood obesity. The variation in a student’s exposure to fast
food restaurants comes in two ways. One, change in the count of restaurants surrounding
schools. Two, students moving to different schools either because of a natural progression
through the public school system or by just relocating within the state and, thereby, to
another school. In this dataset, about 42 percent of the students relocated but remained
in the public schools in Arkansas. A child’s BMI could be influenced by several
environmental factors inside schools, outside of schools, within the family, and within
the community, some of which could be related to the density of fast food restaurants. Our
data allow us to control for several observable factors. However, note that the
coefficient on the number of fast food restaurants takes into account only the covariation
between the restaurant count around the school and BMI z-score. Food intake from home
might bias the coefficient of interest, but we include variables that capture the
commercial food environment around a student’s residence, including distance to nearest
grocery, dollar store, convenience store, fast food, pizzeria and sandwich place. To the
extent household behaviors towards food consumption persist with time, the inclusion of
student-level fixed effects can be advantageous as they difference out unobserved time-
invariant factors that might be correlated with the variable of interest. In terms of the
features of the food environment within schools, all schools were subject to Act 1220 of
2003. Act 1220 required nutrition standards to be applied to all foods and beverages sold
or made available to maintain a healthy school environment. For example, Act 1220 requires
50% vended beverages to be a healthy choice such as water, 100% fruits juice and low-
fat/fat-free milk. Act 1220 was in effect across Arkansas during the entire study period.
Thus, we do not expect wide variation in within school environment across schools in terms
of the food and physical education/activity environment. Other factors within schools
could play some role. For example, peers may influence diet and physical activity choices
that might then influence body weight. One challenge with including peers’ variable is
that it brings with it into the model a host of other biases. As described in Asirvatham
et al. (2018), these biases could further complicate the model. We, therefore, do not
include peers’ weight variable but include school-level percentages of different race
groups and meal status. Both of these are correlated with obesity and, therefore, to some
extent account for peers influence (Boyd et al., 2011). Nevertheless, we acknowledge that
the methods used here can only partially addresses the biases created by unobserved
changes within the school environment during the study period. There could also be common
factors at the community-level that might drive restaurant counts. Consider a town with a
population that does not demand high calorie foods. Such a population might also have
lower restaurant counts in the near vicinity of schools. One implication of such demand is
that the lower income population might demand lower-cost food products, which are often
provided by fast food restaurants. To address all of these biases, we use an instrument
that drives the fast food restaurants’ location choice.

<h>IDENTIFICATION STRATEGIES</h>
-------------------------

We estimate the effect on two samples, one on the whole student population and the other
on a subsample of students who were exogenously reassigned to other schools in response to
a court-mandated reorganization of schools and districts. This allows us to test for
possible mechanisms of the effect and propose some recommendation to reduce its effect on
BMI outcomes. Although complementary, the analyses we conducted using these two samples
provide different insights. We utilized the instrumental variables approach on the larger
student population for whom all information was available, and then exploited a natural
experiment of exogenous school assignment of a subset of students in response to a court-
mandated school restructuring. Below we discuss both methods in detail.

<hs>  Instrumental variable (IV) method</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The instrument we use is the distance of the school to the nearest interstate or US
highway. This has been well established in the literature. Dunn (2010); Anderson and Matsa
(2011), Dunn et al. (2012), and Alviola et al. (2014) use some measure of highway
proximity as an instrumental variable for fast food restaurants. Fast food restaurants
locate in places where there is demand for the products they offer. By locating closer to
highways, fast food restaurants are able to profit from the demand from travelers, but
this could exogenously increases exposure to fast-food restaurants for those living near
major highways, or in our case for schools located close to major highways. The
identifying assumption is that nearness to highway is a factor in restaurant location
decisions. That is, nearness to highway is a factor in restaurant location decisions
because proximity to interstate and US highways might bring in firms supplying services
and products to travelers. Using County Business Patterns data, Dunn (2010) shows that
interstate exits drive the location of fast food establishments in way that is different
from other businesses. He also shows that number of interstate exits is not correlated
with other healthy behaviors, such as fruit and vegetable consumption and physical
activities. Dunn (2010) discusses both aspects of demand and supply that could bias an
estimate. For example, higher demand for fast food could lead to more restaurants. On the
other hand, residents with preference for health could enforce restrictions on location
and number of fast food restaurants. He concludes that the direction of the bias is
generally positive. In our context, schools factoring in distance from state and federal
highways might violate the exclusion restriction. This violation would occur because a
school’s decision and a restaurant’s decision are influenced by the same explanatory
variable. Even though some states do stipulate school construction to be at a distance
from highways, Arkansas only stipulates distance from any source of sound that produces 65
decibels sustained and 75 decibels peak2 . Thus, we argue that the distance of schools
from highway in the context of policies in place in Arkansas does not violate the
exclusion restriction. During our study period, the locations of highways are fixed.
However, students change schools as part of a natural progression through the public-
school system and this creates time series variation in the distance between the child’s
school and highway. The instrument used in the literature, in general, considers only
interstate highway, but due to the sparseness of interstate highways in Arkansas, as shown
by Alviola et al. (2014), we consider both interstate and US highways for our instrument.5
The standard way to include the IV in an equation is to use it as a single variable. In
this study, we include it in two different ways. Firstly, as a single continuous variable.
Secondly, to control for a non-linear relationship, the IV is split into segments based on
different radial distances from the school to the highway. Since we estimate the effect at
one-third, two-thirds, and a mile, the instrument is split into four parts, namely one-
third mile, two-thirds mile, a mile, and more than a mile. A school that is a third of a
mile away from the nearest federal highway will have the specific distance in the sub-
variable for one-third mile, with zeros in other sub-variables. This is tantamount to
relaxing the assumption that the instrument has a unique linear relationship with the
endogenous variable.

<hs>  Exogenous assignment to schools</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In addition to the instrumental variable method, we analyze a subsample of students who
were exogenously assigned to different schools. This subsample of 2739 observations
constitutes a small fraction of the total 1,352,696 observations in the main analysis
sample, but provides a complementary analysis to the IV methods explained above. The
strategy is similar to that pursued by Asirvatham et al. (2018) in their analysis of peer
effects using the Arkansas BMI data. As explained in this earlier study, the exogenous
reassignment was created by a court mandated restructuring of public schools. In 1992, the
Lake View School District and other plaintiffs claimed that the school funding system was
unconstitutional. In the Lake View School District No. 25 v. Huckabee case, the Arkansas
Supreme Court ruled that the state educational funding was unconstitutional. To meet the
court mandate, the State passed the Public Education Reorganization Act, Act 60, during
the Second Extraordinary Session of 2003. School reorganization thus occurred to overhaul
the public school funding system. Since the primary motivation was not to restructure the
schools to improve students’ health and because the legislation was passed in a special
session of the state legislature in response to the court ruling, we posit that this
restructuring created an exogenous school assignment for the students it affected. There
were two ways the State sought to comply with the court decision: either through
consolidation or annexation for all districts with fewer than 350 students. Consolidation
involved cutting administrative overhead by bringing schools and/or school districts under
fewer management personnel. Annexation required physically closing school locations and
have the children attend a nearby school that met the criterion set by the legislature.
Thus, annexation created a change in school of attendance that was plausibly exogenous. An
exogenous reassignment to other schools more directly addresses the issue of self-
selection into schools. This reassignment, we argue, is largely uncorrelated with
observables and unobservables that determine BMI outcomes. This is especially valid
because the students are not in their original school attendance zone, which then largely
rules out common factors or linkages between student BMI outcomes and restaurant location
around their re-assigned school. In the results section, we discuss differences between
annexed schools and reassigned schools.

<h>DATA</h>
----

In an effort to combat high rates of childhood obesity, the Arkansas General Assembly
passed the Act 1220 of 2003. Among other things, this legislation mandated that public
schoolchildren be assessed for BMI beginning in the 2003–2004 school year. BMI screenings
have been ongoing since that time. We use these BMI screenings as the main data source in
this study. The Arkansas Center for Health Improvement (ACHI) led the development and
implementation of the state-wide BMI assessment process.13 ACHI developed a statewide
protocol for standardized measurements across the state. Height and weight measurements
are measured by trained personnel in schools and are reported to ACHI. The dataset we use
includes BMI z-scores, race, gender and participation in free or reduced lunches. These
data also include the weight status of each child, which based on reference growth charts
from the Centers for Disease Control and Prevention (CDC). Only those students with at
least two BMI observations are included in our analysis sample. Medical professionals and
the Centers for Disease Control & Prevention (CDC) use BMI z-scores as a general indicator
to track body weight progress among children. As a child grows, so does his/her body
weight and height. The BMI z-score takes into account this growth and development, which
also differs by sex. The BMI z-score provides a uniform measure of body weight across our
sample that contains children that differ by age and sex. Our empirics are based on a
panel dataset covering the years 2004–2010. One problem we confronted in assembling the
data set is that state policy relating to the frequency of BMI measurement changed during
our study period. From 2004 to 2007, the BMI of school children was measured annually for
all grades. Thereafter, BMI was measured and reported only for children in even-numbered
grades inclusive of kindergarten. Thus, we have BMI prevalence rates for students from all
grades from 2004 through 2007, but only for students in even grades after 2007. The non-
reporting of obesity prevalence in odd grades after 2007 should not bias our estimates,
since the decision to stop measuring the BMI of children in odd-numbered grades was
exogenous in that it was not made by the child, the child’s family, or the child’s school.
However, this change in reporting does affect our ability to take into account BMI changes
in a consistent fashion over time. Another source of data we bring into the analysis is
location of food businesses. These are based on Dun & Bradstreet business lists and
include restaurants, grocers, and other food stores. Details on the construction of the
food environment are provided in the Appendix. Using Geographic Information System (GIS)
software, we create measures of the commercial food environment around schools and
residences. These variables measure the number and type of restaurants at varying radial
distances from schools in the increments of a third of a mile up to a mile. Specifically,
we measure the number of fast food restaurants, sandwich places and pizzerias. Measures of
the food environment around a student’s residence include distance to the nearest grocery
store, dollar store, convenience store, fast food restaurant, pizzeria, and sandwich
place. Fast food restaurant counts may reflect local demand for fast food. To the best of
the authors’ knowledge, all but one school had a “closed campus” policy during the study
period. Seniors in this high school had the option of eating out during the lunch period
with school permission. Students in the sample would not generally have sanctioned access
to fast foods during the school day suggesting that access would be primarily before and
after school hours. We also restricted the sample to those less than 18 years old.

<hs>  Annexed sample</hs>
  ~~~~~~~~~~~~~~

Table 1 presents the summary statistics of the entire population of students included in
the analysis (called the general sample) and also compares it to the students who were
reassigned to a different school (called the annexed sample). Students in the general
sample differ from those students who were reassigned to a different school in certain
characteristics. The BMI z-scores in the annexed sample are 0.05 standard deviations
larger than the overall sample. There is a negligible difference across gender proportion.
Annexed schools, however, had 27 percentage points more African American students and 21
percentage points less Caucasian students. The annexed sample also had a higher percentage
of students qualifying for free lunches, 65% compared to 43% among all schools. In terms
of the commercial food environment, students in annexed schools were further away from all
of the measured food establishments. This sample also had slightly more rural students.
The summary statistics generally reflect the communities that were affected by this school
restructuring process. For instance, this reform closed smaller schools and integrated
them into larger schools. Smaller schools are predominantly in the rural areas. Overall,
differences in school-level demographic characteristics between the general sample and the
annexed schools are markedly different in terms of race, household income, urbanization
and access to some of the most important food establishments. One concern in the
restructuring process is if students were reassigned to schools with similar
characteristics or in similar neighborhoods. Asirvatham et al. (2018) assessed differences
in the schools that closed and the schools to which students from the closed schools were
reassigned. Data on children from the sending schools, i.e., annexed schools, constitute
the second analytic sample we used in our analysis. This exogenous assignment addresses
the issue of self-selection because, had it not been for the annexation, these students
would not otherwise be attending a school outside of their original attendance zone.
Asirvatham et al. (2018) found significant differences in percent free and reduced lunch
between sending schools and receiving schools indicating that the schools differed in
socioeconomic characteristics. However, by the nature of the school restructuring process
and difference in student population characteristics, we can affirm that a student’s
current BMI is unlikely to be correlated with unobserved factors at the new school.

<h>ECONOMETRIC MODEL</h>
-----------------

Our basic model to estimate the effect of fast food restaurants surrounding schools on
student BMI is:Yit = β0 + β1Rk(i)t + β2Xit + β3Xk(i)t + β4Fit + Uikt,where Yit is the BMI
z-score of the ith student in time t; Rk(i)t is the restaurant counts around the kth
school of the ith student at time t; Xit is a vector of student i’s characteristics;
Xk(i)t is a vector depicting demographic student characteristics at the school-level in
school k where student i attends, including proportion of students of different race
categories and gender and percent qualifying for free and reduced lunch; Fit is the vector
of commercial food environment near the residence of student i which includes distance to
nearest grocery, dollar store, convenience store, fast food, pizzeria and sandwich place;
and Ui is the error term which equals μi + εit, where μi is the unobserved time invariant
component and εit is the spherical error term. Variables measuring different aspects of
the commercial food environment around student’s school and residence were constructed
using GIS software and geolocation of the schools, food establishments and student
residence. To tease out the effect of distance of the fast food restaurants from schools,
we developed three variables measuring the number of fast food restaurants within
different radial distances from school, namely one-third of a mile, two-thirds of a mile,
and a mile. Besides the number of restaurants at different radial distances, we also
created two sets of variables with different combinations of restaurants. One included
only fast food restaurants and the other included fast food, sandwiches and pizzerias. The
panel nature of the data and the amount of information on students, schools and food
environment allow us to control for individual and school-level characteristics, and also
to use student-level fixed effects that further reduces the endogeneity bias due to
omitted variables in the estimate. Since there could be year-to-year changes in a
student’s BMI that if not accounted for might bias the estimates, we also estimate a two-
way FE model by adding binary variables for different years in the data period. Thus, the
two-way FE models include both student-level fixed effects and year fixed effects. Note
that the observations are annual so year fixed effects would capture time-invariant year
to year changes in the BMI that are not captured by the included right-hand side
variables.

<h>RESULTS AND DISCUSSION</h>
----------------------

As discussed above, our research objective is to estimate the impact of fast food
restaurants surrounding the schools on a child’s BMI z-score, and check if there are any
differences in the effects by radial distance of restaurants from school. In this section,
we first present results from the pooled OLS (top panel, Table 2) and student fixed
effects models (bottom panel, Table 2). The pooled OLS shows that the effect, though
likely biased, is very small or zero in magnitude and that the sign of the coefficient is
always negative, which is inconsistent with our prior expectation that fast food exposure
should be positively related to BMI. Importantly, healthier parents choosing healthier
neighborhoods might create positive bias. On the supply side, restaurants locating in
neighborhoods with a larger proportion of lower income families might at least show some
restaurant effect. Pooled OLS, however, assumes all observations are independent. Our data
have multiple observations on each student and therefore we are able to obtain within
estimates by controlling for the student-level fixed effects. These results are in the
bottom panel of Table 2. Some of the estimates are positive in sign but are very small in
magnitude. Moreover, results are robust to inclusion of grade effects or additional
controls for food stores around children’s residences. Controlling for the commercial food
environment surrounding the residence of each student had little impact on the estimates
once student-level time-invariant unobserved factors are accounted for. Even though we
control for unobserved time-invariant factors at the student-level beyond the residential
food environment, we cannot entirely rule out the self-selection bias. This could
potentially bias the estimate because parents choose where they live. For example, an
occupation requiring frequent long-distance travel might increase the likelihood of
choosing a residence near highways. As previously discussed, our first identification
strategy is to instrument for the restaurant counts. Results from fixed effects IV method
are presented in Tables 3 and 4. The heteroskedasticity-robust first stage regression
results in Table 3 indicate that average distance of schools from federal highways (the
instrument) is a very significant and strong predictor of restaurant counts surrounding
schools. The negative coefficient indicates that the number of restaurants decrease as the
distance of the school from the highway increases. Large F-statistics are indicative of
high correlation between restaurants counts and the instrument. On the smallness of the
magnitude, it should be noted that more than 50% of the schools did not have restaurants
within the certain defined radii at some point during the study period. The sign suggests
that the farther the average distance of a school from nearest highway, the lesser is the
number of restaurants locating near schools. The reduced form fixed effects regression
also yielded significant estimates of the instrument. Despite the absence of fast food
restaurants for a large number of schools, the magnitude at one-third radial distance
suggests a 2.1 percent increase in BMI z-score, 0.0147 standard deviations from the mean
0.704 SD. At a two-thirds mile radial distance, the estimate decreased by a third and at a
mile radius, the estimate further decreases by a fifth. The instrumental variables
estimates show interesting results. First, the general result is that restaurants around
any defined radii have at least some effect on student BMI. Second, within the same group
of restaurants, the effect decreases as the radial distance increases. This reflects the
fact that as a restaurant locates further away from a school, its influence on BMI begins
to wane. This could indicate the reduced effect on calorie intake as distance from a
school increases or that distance from school does matter – even though the effect is
small. Thirdly, among different groups in general, the estimate is higher when the fast
food measure excludes sandwich places and pizzerias. At a third of a mile radius, fast
food restaurants alone show an increase of 0.024 standard deviations in BMI z-score
compared to 0.015. This seems counterintuitive, but keep in mind that only about 50% of
the schools had fast food restaurants. This relatively smaller magnitude could indicate
that the effect of sandwich places and pizzerias might be much lower than the fast foods
itself. Thus, the IV method finds a very modest effect of the restaurants surrounding
schools on a student’s BMI. Our complementary analysis of the annexed sample is consistent
with the findings above in that there is no evidence of a large fast-food effect on BMI
(Table 5). It is much smaller. Both OLS and fixed effects estimates show no significant
effect at any radial distance from the school. The observations on reassigned students
constituted less than a quarter percent of the total observations used in the analysis
above. The regression model used to the obtain the results in Table 3 include similar
control variables to the those used in the panel IV models reported above. As discussed
above, this sample is different from the general sample analyzed in several respects.
Those differences could partly explain why no effect is observed in the annexed sample
compared to only a marginal effect in the general sample. Compared to the general sample
students in the annexed sample had to travel further away because the school in their
attendance zone closed which may have prevented access to restaurants before and after
school-hours. The OLS and the fixed effects estimates show high standard errors. The
results presented so far analyze all students and include several covariates that might
influence a student’s BMI. In the Appendix, we ran additional regressions to examine if
the restaurant effect might vary by age or by geographic areas based on city centers or
population densities. Specifically, specifications based on age group present estimates
for elementary, middle, and high schools (Tables A1–A3, respectively). Estimates from
regressions for rural and urban schools are presented in Tables A4 and A5, respectively.
The results show some differences by age but nothing of economic significance. The main
conclusions of the paper appear to hold across the different age categories. We also do
not find any difference across rural and urban areas.

<h>CONCLUSIONS</h>
-----------

In this study, we estimate the effect of the number of fast food restaurants surrounding
schools on the body mass index (BMI) z-score of school children. The study uses
individual-level panel data from students attending public schools in Arkansas. The
results from the two methods on two samples drawn from the same student population are
similar. First, an instrumental variable strategy is employed using an instrument that has
been validated by previous studies. A school’s distance from the nearest highway is used
to instrument for the endogenous variable of interest, the restaurant count surrounding
the school at specified radial distances. The identifying assumption is that fast food
restaurants located by the highways cater to the highway travelers. We use the same
instrument in two ways for efficient estimation. In the first specification, we use a
single variable. In the other specification, we separate the instrumental variable into
parts based on its distance from the highways. The same instrument is used in two
different specifications, and both arrive at similar results. Second, we exploit a natural
experiment that resulted when a number of Arkansas schools were reorganized in response to
a state Supreme Court decision on school funding. This created an exogenous reassignment
of students to schools other than the one in their attendance zone. Students in this
exogenously assigned sample have different exposure to restaurants surrounding schools. In
fact, given their distance and time to travel to a school that is located further away, it
is unlikely that they would have had the opportunity to visit a fast food restaurant while
taking the school bus. Thus, the two estimates, although complementary, have different
implications. This study finds the effect of restaurants surrounding schools on childhood
obesity to be negligible. Our point estimate, while very small, is highly significant. The
smaller estimate might cultivate a laissez-faire attitude towards regulating restaurants
around schools, but the findings reported here must be interpreted within the context of
the study. Most Arkansas schools to had closed campus policies during the study period
that meant children would only have access to outside restaurant food before or after
school hours. Hence, replicating our study in other contexts to test the robustness of our
findings would be warranted.

<h>FUNDING</h>
-------

This research was funded by the Agriculture and Food Research Initiative of the USDA
National Institute of Food and Agriculture, grant number 2011-68001-30014. This work was
also partly supported by the National Research Foundation of Korea (NRF-2014S1A3A2044459);
Research Council of Norway Grant #233800; the Arkansas Biosciences Institute (ABI); and
the National Institute of General Medical Sciences of the National Institutes of Health
under Award Number P20GM109096. The research reported in this study was approved by the
Institutional Review Board, University of Arkansas, Fayetteville, USA under protocols #
10-11-235 and # 14-07-026. The procedures of this study are in accordance with ethical
standards for human research.


<h>REFERENCES</h>
----------

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  [2] Michael L. Anderson, David A. Matsa. Are restaurants really supersizing America?. doi:10.1257/app.3.1.152
  [3] S. Bryn Austin, Steven J. Melly, Brisa N. Sanchez, Aarti Patel, Stephen Buka, Steven L. Gortmaker. Clustering of fast-food restaurants around schools: A novel application of spatial statistics to the study of food environments. doi:10.2105/AJPH.2004.056341
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  [6] Thomas Burgoine, Nita G. Forouhi, Simon J. Griffin, Nicholas J. Wareham, Pablo Monsivais. Associations between exposure to takeaway food outlets, takeaway food consumption, and body weight in Cambridgeshire, UK: Population based, cross sectional study. doi:10.1136/bmj.g1464
  [7] Janet Currie, Stefano Della Vigna, Enrico Moretti, Vikram Pathania. The effect of fast food restaurants on obesity and weight gain. doi:10.1257/pol.2.3.32
  [8] Brennan Davis, Christopher Carpenter. Proximity of fast-food restaurants to schools and adolescent obesity. doi:10.2105/AJPH.2008.137638
  [9] Richard A. Dunn. The effect of fast-food availability on obesity: An analysis by gender, race, and residential location. doi:10.1093/ajae/aaq041
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  [11] Jared Jashinsky, Jennifer Gay, Nathan Hansen, Jessica Muilenburg. Differences in TV Viewing and Computer Game Playing’s Relationships with Physical Activity and Eating Behaviors among Adolescents: An NHANES Study. doi:10.1080/19325037.2016.1250017
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<ART>Early life height and weight production functions with endogenous energy and protein inputs
================================================================================

Authors: Esteban Puentes, Fan Wang, Jere R. Behrman, Flavio Cunha, John Hoddinott, John A. Maluccio, Linda S. Adair, Judith B. Borja, Reynaldo Martorell, Aryeh D. Stein
DOI: 10.1016/j.ehb.2016.03.002
Year: 2016  |  Pages: 65-81
ASJC codes: 2001
Keywords: Early childhood, Endogeneity of inputs, Growth Proteins, Nutrition

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We examine effects of protein and energy intakes on height and weight growth for children between 6 and 24 months old in Guatemala and the Philippines. Using instrumental variables to control for endogeneity and estimating multiple specifications, we find that protein intake plays an important and positive role in height and weight growth in the 6-24 month period. Energy from other macronutrients, however, does not have a robust relation with these two anthropometric measures. Our estimates indicate that in contexts with substantial child undernutrition, increases in protein-rich food intake in the first 24 months can have important growth effects, which previous studies indicate are related significantly to a range of outcomes over the life cycle.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Inadequate child growth and weight gain are of paramount concern. Approximately 165
million children under five years old in developing countries are stunted and 100 million
are underweight (Black et al. (2013)). Growing evidence indicates that early-life
undernutrition is associated with, and likely in part causes, reduced education, adult
cognitive skills, and wages (Grantham-McGregor et al., 2007; Engle et al., 2007, 2011;
Victora et al., 2008; Hoddinott et al., 2008, 2013; Behrman et al., 2009; Maluccio et al.,
2009). Despite widespread concern about early-life undernutrition there is limited
systematic knowledge about production technologies for key outcomes, particularly height
and weight, needed to inform more-effective program and policy design. This gap is
partially due to inherent difficulties in modeling these complex biological and behavioral
processes—often strong assumptions are required for estimation, so that it is difficult to
make definitive conclusions. A major challenge in estimating production functions for
height and weight is that inputs reflect behavioral choices. Using data from the same
Philippine study analyzed in this paper, Akin et al. (1992) and Liu et al. (2009) find
that families allocate nutrients to compensate for prior poor health. Where allocations
reflect compensatory behaviors that are not controlled for in the estimation, the
estimated effect of nutrients on growth can be biased. Another challenge is measurement
error in inputs. Using related data from Guatemala, Griffen (2016) finds that estimates of
energy effects on height are substantially larger using instrumental variables (IV) than
with ordinary least squares (OLS) probably in part due to measurement error. In this
paper, we examine relations between energy intake and: (1) linear growth and (2) weight
gain. We use longitudinal data from Guatemala and the Philippines that includes detailed
information on anthropometric outcomes, nutrition and other inputs collected at intervals
of two-three months to estimate height and weight production functions for children in the
critical age range 6–24 months. In our specifications, height and weight depend on lagged
height and weight, energy intakes, breastfeeding, diarrhea, and individual fixed
endowments. We combine individual fixed-effects (FE) with instrumental variables (IV) to
control for both endogeneity and measurement error. This paper presents three important
methodological contributions. First, we estimate production functions for two countries,
Guatemala and the Philippines, and for two anthropometric measures, height and weight,
which allows us to compare the robustness of our findings across different settings and
anthropometric outcomes. Second, we improve on previous IV literature on growth by
providing details of instrument selection and an assessment of how the results are robust
to changes in the instrument set. We present estimates for numerous instrument
combinations, putting emphasis on those judged more reliable based on over-identification
and weak instrument tests. Third, in addition to considering total energy intake, which is
the nutritional input usually considered in the economics literature, we disaggregate
energy intake into two components: proteins and (all) other macronutrients (which we refer
to as “non-proteins”, meaning fat and carbohydrates). This emphasis on dietary quality,
highlighted by Arimond and Ruel (2004), is especially relevant because it may help design
interventions that better reduce stunting and underweight. We find robust and positive
effects of proteins on height and weight growth. Energy from other macronutrient
consumption (non-proteins), is not systematically related to these anthropometric
measures, which suggests that protein-rich foods are particularly important for growth of
undernourished children.

<hs>  Input selection</hs>
  ~~~~~~~~~~~~~~~

Our choice of inputs is guided by Black et al. (2008) who argue that inadequate diet and
disease are the main immediate causes of stunting and wasting. With respect to diet, two
energy sources have been identified as being especially important for child growth:
proteins and non-protein energy from other macronutrients. Infants require certain minimum
amounts of energy and proteins to maintain long-term good health but these requirements
are heterogeneous and depend on several factors including weight and whether the child is
breastfed (FAO, 2001; WHO, 2007). Children's energy requirements are partly driven by
energy costs of linear growth, which has two components: (1) energy needed to synthesize
growing tissues and (2) energy stored in these tissues (FAO, 2001). These comprise
approximately one-third of total energy requirements during the first three months of
life, but despite increasing in absolute terms they decline to only 3% by age 24 months,
in part because overall energy requirements increase substantially with body size.
Proteins are needed to balance nitrogen loss, maintain the body's muscle mass, and fulfill
needs related to tissue deposition (WHO, 2007). There is also evidence from research on
animals that protein provides anabolic drive for linear bone growth (WHO, 2007).2 To study
the relative importance of protein and non-protein sources, we first examine the
relationship between total energy and height and weight and then consider the potential
for separate roles of the two at once in a single growth model. The comparison of proteins
with non-proteins highlights the relative importance of proteins in children's diets and
informs what types of interventions might have greater impact on height and weight.3 There
is a limited literature focused on the distinction between total energy and protein
energy. Pucilowska et al. (1993) find that high-protein supplementation in Bangladeshi
children with shigellosis, a severe bacterial disease, increased weight compared to normal
protein diets. A randomized evaluation for children up to 2 years of age in several
European countries demonstrated that receiving baby formula with high protein content (%
calories from protein) increased weight, but not height (Koletzko et al. (2009)). Both of
these study populations, however, are different from the ones we examine. The Bangladeshi
sample is restricted to children recovering from shigellosis while the European sample had
not experienced the same nutritional deficiencies found in our samples. Using a sample
more similar to ours, Moradi (2010) finds that access to high-quality protein, such as
from livestock farming, better predicts height in some African countries than other energy
sources. Similarly, Baten and Blum (2014), using global information for the first part of
the twentieth century, that includes Guatemala and the Philippines, also find that local
availability of cattle, milk and meat were an important predictor of adult height.4 A
related issue is protein quality. Proteins are composed of amino acids with specific cell
functions, and amino acid content defines protein quality. For instance, plant-based
proteins lack essential amino acids unlike animal-based proteins (Dewey, 2013). In
addition, plant-based diets have high levels of phytic acid, which might inhibit zinc
absorption (Gibson, 2006), and zinc plays a key role in cellular growth and
differentiation (Imdad and Bhutta, 2011). For animal-based protein, Mølgaard et al. (2011)
argue that dairy intake has positive impacts on child growth. Although the mechanism is
not entirely clear, this may be due to the stimulating effect on plasma insulin-like
growth factor (IGF-1) (Michaelsen, 2013). Breastfeeding is another critically important
source of nutrition in early life (Black et al., 2013). In this paper, we have data on
breastfeeding status but not on the amount of breast milk consumed. Thus, our energy
intake measures exclude energy from breastmilk requiring us to control for breastfeeding
status in the models. Among diseases that affect growth, Walker et al. (2011) suggest that
persistent diarrhea and other diseases can have long-lasting effects on children's
physical development. Therefore, in our analyses, we incorporate diarrhea as an input, as
it is considered a major contributor to stunting, wasting and child mortality (Black et
al., 2013).

<hs>  Height and weight production functions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The main challenges for estimating height and weight production functions include the
endogeneity of inputs and measurement error (Behrman and Deolalikar, 1988). To overcome
these, we follow the general approach developed in recent research on production function
estimation for cognitive and non-cognitive skills (Todd and Wolpin, 2003, 2007; Cunha and
Heckman, 2007). Because they include individual fixed effects and the entire input
history, Eqs. (1) and (2) are difficult to estimate. For example, if inputs are treated as
endogenous and an IV approach were used, it would be necessary to have at least one
instrument for each period in the entire input history. Thus, instead of directly
estimating these two equations, we make two further assumptions that allow less demanding
specifications in terms of data and instrument requirements, while remaining more flexible
than previous specifications in the literature. Effects of past inputs follow a monotonic
(likely decreasing) pattern at a constant rate γ for each period.5 That is: βt−j = γβt−1−j
and δt−j = γδt−1−j. The coefficients on inputs in the height function are the same as
those in the weight function, up to a multiplicative constant δt−1−j = ((1 + σ)/α)βt−1−j.
Together, these assumptions reduce the set of endogenous variables to a tractable number,
thereby reducing the number of required instrumental variables. Under these assumptions,
height growth can be expressed as a function of current inputs, past height and weight,
and an error involving current (t) and previous period (t − 1) shocks. Current inputs
enter directly; the full history of past inputs enter indirectly through the lagged height
and weight. As with the change-in-height Eq. (3), the change-in-weight Eq. (4) depends on
current inputs, past height and weight, and an error including current and previous period
shocks.6 This framework forms the core of our approach to estimating production functions
for height and weight. Estimation of Eqs. (3) and (4) allow recovering β0 from Eq. (1) and
δ0 from (2).

<hs>  Estimation and identification</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Although differencing removes individual-level fixed effects and thus controls for
important sources of potential bias (unobserved persistent heterogeneity including, e.g.,
genetic endowments and fixed parental and household characteristics), to consistently
estimate the parameters in the relations for change in height (Eq. (3)) and change in
weight (Eq. (4)), we still need to overcome several endogeneity problems. First, by
construction previous height and weight are correlated with the error terms of Eqs. (3)
and (4) (see Eqs. (1) and (2)). Moreover, if we assume that the household responds to past
shocks as is likely and for which there is evidence for the Philippines (Akin et al.,
1992; Liu et al., 2009), current inputs may be correlated with the error terms. We address
potential endogeneity by using IV, which also addresses bias due to random measurement
error in x under the assumption that the instruments are uncorrelated with that
measurement error. The set of candidate instruments we use differs by country but draws on
plausibly exogenous factors including a randomized intervention in Guatemala and prices of
common foods in both countries. We treat market prices as exogenous to households (as in
Liu et al. (2009)). Using prices as instruments for inputs is a well-established approach
in the estimation of production functions (Todd and Wolpin (2003)). We also include past
height and weight measures, hi,t−2 and wi,t−2 as instruments to help identify the effects
of lagged height and weight. (Instruments are described in further detail in Section 3.3.)
Using the available instruments, we endogenize protein and non-protein intakes, as well as
lagged height and weight. However, we do not have access to instruments in both countries
that also would allow us to control for the potential endogeneity of breastfeeding or
diarrhea.7 Controlling for individual-level fixed effects is an important aspect of our
approach, however, and goes part way toward addressing their potential endogeneity. For
example, fixed effects control for the possibility that certain children have a pre-
disposition for diarrhea, or live in particularly unsanitary households. However, if
households change breastfeeding practices when health shocks affect their children's
health or change sanitary conditions to reduce the diarrhea prevalence, the estimated
effects of breastfeeding and diarrhea could be downward-biased. For instance, households
that have increased breastfeeding could be compensating for negative health shocks,
suggesting a negative relationship between growth and breastfeeding, while correcting for
endogeneity could show a positive relationship (and similarly for diarrhea). Because our
principal objective is to study the roles of proteins and non-proteins in the production
functions, however, we do not emphasize the coefficients for diarrhea and breastfeeding
but instead make clear the assumptions under which our primary coefficients of interest
are consistently estimated even if breastfeeding or diarrhea are endogenous in the model.
Our estimation approach is consistent provided the instruments are not correlated with the
error term in the production function, conditional on breastfeeding and diarrhea as well
as other covariates mentioned below. This is plausible for the same reason that the
instruments are exogenous in relation to the energy inputs, e.g., that they are not
correlated with individual-level time-varying health shocks.8 In principle, there also
could be interactions among inputs in the production function, such as between nutrient
intakes and diarrhea, or between breastfeeding and other nutrient intakes but a
specification incorporating such interactions would be even more challenging to estimate,
requiring additional instruments. Given that there are already four variables that we
treat as endogenous in our main models (protein, non-protein, lagged height, and lagged
weight), we do not estimate models with such potential interactions; instead, we studied
possible interactions by splitting the sample. For instance, to examine whether diarrhea
or breastfeeding interacts with diets, we estimated specifications for the sample that is
breastfed and compare the results with the sample that is not breastfed. We carried out a
similar exercise for diarrhea. Our results indicate that coefficients are not affected
when we separate the sample by breastfeeding types. For diarrhea, there was some evidence
of interaction effects, where diarrhea lowers the effects of macronutrients, but because
most of the specifications suffer from problems of weak instruments, we are unable to draw
strong conclusions. The estimation of the growth equations also includes an indicator for
whether the child was female, number of days since the previous measurement, and age and
age squared at time t. Our methods permit us to improve upon the previous literature that
investigates the effects of total energy on anthropometrics. Since we do not have a single
set of preferred instruments, we are able to robustly study effects of total energy on
height and weight across two settings. We do this estimating the changes in height and
weight, first using total energy intakes and then separating protein and energy from other
macronutrient intakes to examine their relative partial effects in each model.

<h>DATA</h>
----

Estimation of (5) and (6) requires high-frequency longitudinal data in early life that
contain information on the outcomes (height9 and weight) and inputs (proteins and other
macronutrients, breastfeeding, and diarrhea), as well as plausibly exogenous instruments.
We now describe the data and contexts for two unique studies that fulfill these
substantial requirements relatively well, one in Guatemala from the 1970s and the other in
the Philippines from the 1980s.

<hs>  Guatemala</hs>
  ~~~~~~~~~

We use data from The Institute of Nutrition of Central America and Panama (INCAP)
1969–1977 nutritional supplementation trial. Four rural villages from eastern Guatemala
were selected, one relatively large pair (∼900 residents) and one smaller pair (∼500
residents). At the outset, the villages were similar in terms of child nutritional status,
measured as height at age three years, and were highly malnourished with over 50% of
children severely stunted, i.e., with height-for-age z-score <−3. One large and one small
village were randomly selected to receive a high-protein supplement (Atole); the others
received an alternative supplement devoid of protein (Fresco). A 180 ml serving of Atole
contained 11.5 grams of protein and 163 kcal. Fresco had no protein and a 180 ml serving
had 59 kcal. The main hypothesis was that increased protein would accelerate mental
development; additionally, it was expected that the high-protein nutritional supplement
would affect physical growth. The nutritional supplements were distributed in centrally-
located feeding centers in each village (Habicht et al., 1995). Virtually all (>98%)
families participated (Martorell et al. (1995)). From 1969 to 1977, anthropometric
measures (height and weight) were taken every three months for all children 24 months of
age or under (including newborns entering the study) in the four villages. This yields a
maximum usable sample for our analyses of 878 children measured at least twice by the age
of 24 months. The amount of supplement intake was recorded daily in all villages. Home
dietary information was collected every three months, including the types and amounts
(except for breastmilk) of all foods and liquids consumed. These dietary histories were
based on a 24-h recall period in the larger villages and a 72-h period in the smaller
villages (from which we construct daily averages), and permit calculation of protein and
non-protein intakes for the 24-h period by summing the nutritional content for each food
item. The survey recorded the total months a child was breastfed. Nutrients from
breastfeeding were not included in the nutritional intake calculations. Retrospective
information on illness, specifically the length in days of episodes of diarrhea and fever,
was collected semi-monthly.

<hs>  The Philippines</hs>
  ~~~~~~~~~~~~~~~

We use the Cebu Longitudinal Health and Nutritional Survey, a survey of Filipino children
born between May 1983 and April 1984 in 33 rural and urban communities (barangays) in
Metropolitan Cebu. The baseline survey included 3327 women sampled at a median of 30 weeks
of gestation, and yielded a sample of 3080 singleton live births. This sample also
exhibits high levels of undernutrition; at age 24 months, 62% of the children were stunted
and 32% underweight. During the first two years of each child's life, data were collected
every two months. This included anthropometric measurements, 24-h dietary recall of types
and amounts (except breast milk) of all foods and liquids eaten, breastfeeding, and recent
illness history. For breastfed children, the survey also collected the frequency and
length of time spent breastfeeding. Total protein and energy intakes were calculated from
foods consumed the previous day (24-h recall method). At each survey, mothers reported
whether the child had diarrhea in the past 24 h, and if so, when the episode began, and
the number of days the child had diarrhea during the previous week (Adair et al., 2011).
The maximum usable sample of children between 6 and 24 months of age for the Philippines
is 2713.

<hs>  Variable construction</hs>
  ~~~~~~~~~~~~~~~~~~~~~

Linear growth and weight gain are calculated as the difference between consecutive
measurements. Although measurements were scheduled at specified intervals (every three
months in Guatemala, every two in the Philippines), there were deviations including
instances where a scheduled measurement did not occur. Because children experience high
growth and growth spurts during the first two years of life, even differences of several
days can be associated with significant differences in growth. We account for this by
controlling for the exact number of days between measurements. Ideal data for this
analysis would have information on protein and non-protein intakes over the entire period
between measurements, but even in these uniquely comprehensive studies such detailed
information is not available. Therefore, we approximate intakes over the entire period by
using the average of the 24-h intakes calculated from the dietary recall information at
the beginning and end of each period (which decreases measurement error relative to using
only one point in time) multiplied by the exact number of days between measurements. For
Guatemala, we add to this figure the intakes from the supplement (which were measured
daily throughout the period) to obtain total protein and other intakes (as well as their
sum, measured as total energy).10 For breastfeeding, we create a dummy indicator for
whether the child was breastfed in the month previous to measurement at time t. While this
does not fully exploit the detailed information available for the Philippines, it is done
to have similar specifications across countries. The final input we include is diarrhea.
For Guatemala, the protocol was to collect information every 15 days, so it is possible to
construct the number of days experiencing diarrhea for the complete periods between
anthropometric measurements.11 For the Philippines, it is only possible to construct the
number of days with diarrhea during the week previous to each bimonthly anthropometric
measurement. To extrapolate this to the full period between measurements, we estimate a
count model for number of days with diarrhea for each two-month period with the Guatemalan
data and use the estimated parameters from that model to predict number of days each
Filipino child had diarrhea in each two-month period.12 As outlined in Section 2.3, in our
main specifications we instrument for protein, other macronutrient intakes, and lagged
height and weight. We now describe in detail the other instruments besides twice lagged
height and weight. In both countries we use unit prices for various food items, selected
with emphasis on foods with high protein content and/or important in the local diet. For
Guatemala, prices are averages of national-level prices measured during December each
year. We use lagged prices of eggs, chicken, pork, beef, dry beans, corn, and rice. Unit
price variables for Guatemala are deflated and measured over the eight-year study period.
For the Philippines, we use community-specific prices collected as part of the broader
study. Between January 1983 and May 1986, enumerators visited two stores in each
community, every other month, and collected prices (and quantity units) for a list of
items. Not all items, however, were sold at each store at each visit. Consequently, there
is not a complete set of prices for each item from each store (or even from each community
in instances where no price was available from either store) in each measurement period.
We selected as instruments the prices of dried fish, eggs, corn and tomatoes since these
are the ones with the highest frequency in the sample.13 We use both current and lagged
prices of those selected food items. By estimating a large set of instrument combinations,
our approach does not depend on any one particular price, avoiding subjective instrument
selection. For Guatemala, we also exploit the experimental variation resulting from the
randomized allocation. We use a dummy variable that indicates whether the village had a
feeding center that provided the high-protein supplement. We also interact this indicator
with the distance from the home of the child to that feeding center. While the presence of
a randomized allocation of a high-protein supplement provides an important source of
exogenous variation, since there are four endogenous variables, additional instrumental
variables also are used, i.e., twice lagged anthropometrics and food prices. For the
Philippines we rely on price variation, which, unlike the annual Guatemalan food price
data, varies both within-years and spatially, with information on these food items for the
majority of measurement periods and each of the 33 communities.

<hs>  Descriptive statistics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

Over the period from ages 6 to 24 months, each Guatemalan child is observed an average of
4.3 times and each Filipino child 9.1 times. The sample we describe includes all
observations (measurements of children at different ages) with complete information for
the following variables: change in height between consecutive measurement periods (linear
growth), change in weight between consecutive periods (weight gain), total energy, energy
from protein, energy from non-protein, breastfeeding indicator, and days with diarrhea.14
The final number of observations used in each specification varies depending on the
availability of the instrumental variables used in that specification, since instruments
for some observations are missing. Table 1 compares the main variables for both samples.
On average and at all ages, the Filipino children in the early 1980s were taller than the
Guatemalan children in the 1970s. For example, at 12 months of age, Filipino children were
on average 70.7 cm tall, while their Guatemalan counterparts were 1.8 cm shorter. In terms
of average weight, however, there were no significant differences between countries—at 24
months, children from both countries averaged 9.8 kg. 44% of the Guatemalan children were
stunted, and 27% underweight. The corresponding levels were lower, 25% and 11%, for
Filipino children. In 2011 for low- and middle-income countries, average levels of
stunting were 28% and of underweight 17%, and 36% and 18% in Africa (Black et al., 2013).
With broadly similar levels of stunting and underweight, thus, our historical samples
remain relevant to understanding undernutrition in many countries and regions. Table 2
shows that Guatemalan children appear more likely to have been breastfed at all ages. In
both countries, breastfeeding declines with age. At six months, 99% of Guatemalan children
were breastfed, while at 24 months only 18% were; the proportions were 76% and 14% for
Filipino children. Patterns between diarrhea and age are less clear. In Guatemala, average
number of days with diarrhea (per 3-month measurement period) increases with age to 15
months, after which it declines. Levels are relatively lower in the Philippines,
fluctuating between about 2 and 6 days (per 2-month period), with no clear age pattern.
For Guatemala, information is complete on all of the instruments except the distance to
the feeding center, which is missing for ∼5% of observations. For the Philippines, on the
other hand, incomplete price availability leads to larger reductions in the sample size.
The potential sample has 24,820 child-age observations; the lagged price of corn, which is
the most complete, has 18,710 observations and the lagged price of tomatoes, the least
complete, has 16,084 observations.

<hs>  Overview</hs>
  ~~~~~~~~

We estimate height and production functions for children 6–24 months, the period widely
considered to be a critical window for post-birth nutritional investment.15 We use
Generalized Method of Moments (GMM) for exactly-identified models and Limited Information
Maximum Likelihood (LIML) for over-identified models because the latter allows for smaller
finite-sample bias (Stock and Yogo, 2005). As noted, we cluster error terms at the
individual level to take into account correlation of individual error terms and serial
correlation (Baum et al., 2007).16 We first estimate height and weight production
functions using only total energy (i.e., the sum of calories from protein and other
sources), then we analyze separately the roles of proteins and non-proteins. In all
specifications, the energy intakes, lagged height, and lagged weight are treated as
endogenous, and we control for breastfeeding, number of days without diarrhea since the
previous measurement, child sex, number of days since the previous measurement, and age
and age squared. Because there are many potential instrument combinations, to establish
general results that do not depend on one specific instrument combination, we estimated
large subsets of all possible combinations. For Guatemala we first restricted the
instrument sets to combinations that always had the Atole experiment indicator. Then, we
systematically varied inclusion of distance interactions with Atole indicator, second lags
of height, second lags of weight, and from two to four of the seven food prices (eggs,
chicken, pork, beef, rice, beans and corn). For the Philippines, we systematically varied
inclusion of second lags of height, second lags of weight, and from two to six of the
eight (four current and four lagged) food prices (eggs, fish, tomatoes and corn). A
summary of our instrument combinations is found in the Data Appendix Section 6. For
Guatemala, there are 546 specifications (i.e., each with a different instrument set) for
the version of the model with total energy (Eq. (5)) and 525 when proteins and non-
proteins are included separately (Eq. (6)).17 The total number of specifications estimated
for the Philippines is 602 for both models. For each specification, we calculate the
robust versions of the Hansen-J (HJ) over-identification test, the Anderson–Rubin under-
identification test (Anderson and Rubin, 1949), and the Wald F-statistic (robust
Cragg–Donald or CD statistic) to detect weak instruments. Since our main models have four
endogenous variables and we estimate them assuming heterokedasticity, it is not possible
to compare CD statistics with critical values from Stock and Yogo (2005). The robust
versions of these tests were developed in Kleibergen and Paap (2006). We also calculate
for each endogenous variable Angrist and Pischke's (AP) partial F (Angrist and Pischke,
2009), which are informative about the presence of weak instruments. Finally, for all
over-identified models we calculate the Hausman test of equality of OLS and IV estimates.
Since each production function is estimated multiple times, we explore distributions of
estimated coefficients rather than a single or small set of “preferred” specifications,
allowing us to draw more general conclusions. We do not choose or define a preferred
specification because there are no obvious criteria for doing so and because of the
concern that any potential preferred specification would not be robust to changes in the
set of instruments. Although a priori the instruments we propose are plausibly exogenous
and strong, we put relatively more confidence in those instrument sets that better satisfy
over-identification and weak instrument tests. The results of each type of specification
are presented in Tables 3–6 and Figs. 1–3. In Tables 3 and 5, and Fig. 1, we present the
estimated overall energy coefficients. In Tables 4 and 6 (Panels A and B), and Fig. 2, we
present the estimated protein coefficients, and in Tables 4 and 6 (Panels C and D), and
Fig. 3, the estimated non-protein coefficients. Each table presents the 25th, 50th and
75th percentiles of the estimated coefficient distributions and, in the final two columns,
the percentages of the coefficient estimates that are significantly (p < 0.05) positive or
negative. For each Panel in each table, the first row reports distributions for all
estimated specifications and, in subsequent rows, for specifications that are over-
identified, and for those that have HJ P-values > 0.05 and CD statistics > 1, 3, or 7
(provided there are more than 10 such specifications in each case).19 These sets of
specifications focus on results for which relatively strong and exogenous instruments are
available. Figs. 1–3 present point estimates (and associated 95% confidence intervals) for
all specifications that have HJ P-values > 0.05 and CD > 1 (corresponding to the third
rows in Tables 3–6). The scale of the x-axis corresponds to the natural logarithm of CD
statistics and the y-axis the coefficient values.20 To facilitate interpretation of the
coefficient magnitudes, we simulate changes in height and weight when energy intakes
increase ceteris paribus For this exercise, we use the most restrictive specifications
with CD > 7 (or CD > 3 if there are fewer than ten specifications with CD > 7) and HJ
P-values > 0.05. Within that set of specifications, we select the median coefficient and
simulate effects of increasing energy intakes by 300 kcal per day, protein intakes by 10 g
per day, or non-protein intakes by 250 kcal per day. Each of these is approximately one SD
of respective intakes of 18-month old infants in both countries. This hypothetical daily
increase is then multiplied by 90 in Guatemala and by 60 in the Philippines to approximate
total intakes for a given measurement period, and then multiplied by corresponding
coefficients to obtain anthropometric changes. We call this exercise median prediction.

<hs>  Guatemala</hs>
  ~~~~~~~~~

Table 3 summarizes for Guatemala distributions of coefficient estimates on total energy in
the height and weight equations, and Fig. 1A and B show the coefficients and confidence
intervals for the corresponding specifications with CD > 1. Total energy positively
affects height and weight changes. These positive relationships are most evident for
specifications with relatively stronger and more exogenous instruments. Our findings are
consistent with previous literature that uses stronger identification assumptions
estimating similar relationships from the same data sources (Habicht et al., 1995;
Griffen, 2016). For height in Guatemala, estimated coefficients on total energy are
positive in the vast majority of cases, positive and significant (p < 0.05) in 35% of
cases, and never negative and significant. The positive relationship is more robust when
we consider specifications with relatively stronger and more exogenous instruments,
according to the tests. Restricting to over-identified specifications in which HJ P-values
> 0.05 and CD > 3, total energy coefficient estimates are positive and significant 57% of
the time. To provide further interpretation of the magnitude of the coefficients, we
calculate the median prediction (Section 4.1), taking the median coefficient of the
specifications with CD > 3; we calculate the effect of increasing energy per day by 300
kcal. For Guatemala, this implies a 0.62 cm predicted change in height. For weight
production functions, estimated coefficients on total energy are positive and significant
for 36% of specifications, and are never significantly negative. Specifications with
higher CD statistics have larger proportions of positive significant coefficient
estimates. Fig. 1B shows that while there are fewer specifications with higher CD
statistic levels compared to the height model, for those with stronger instruments, the
estimates are generally positive. The median prediction exercise indicates increasing
energy intake by 300 kcal per day yields a predicted 620 g change in weight. Next, we
consider the roles of protein and non-protein energy separately in the growth model.
Proteins robustly and positively affect growth in height and weight in Guatemala, but the
relationship of non-proteins (after controlling for protein) with these anthropometric
measures is non-positive. Panel A of Table 4 (and Fig. 2A) shows that for 53% of all
specifications, protein coefficient estimates are positive and significant. In
specifications with CD > 3, the estimates are always positive and significant. In
specifications with stronger instruments, the estimated coefficient dispersion (i.e., the
distance between the 25th and 75th percentiles) decreases; for specifications with CD > 1
the ratio of the coefficients in the 75th and 25th percentiles is 1.3, while for the
specifications with CD > 3 the ratio is 1.06. Our median prediction exercise indicates
that if protein were to increase by 10 g per day, the predicted change in height is 0.39
cm. For weight change (Panel B of Table 4 and Fig. 2B), we find an even more robust
pattern for proteins. In nearly all specifications (92%), protein coefficient estimates
are positive and significant, and for specifications with CD > 1, they are always positive
and significant. For all specifications, the estimate at the 75th percentile is only 1.2
times larger than that at the 25th percentile. This pattern of stability and significance
of coefficient estimates also can be seen in Fig. 2B where the dispersion of the estimated
coefficients is small, and there is a clear pattern of positive and significant effects of
protein intake on weight growth. An increment in protein intake of 10 g per day results in
a predicted 195 g change in weight. By contrast, there is little evidence that energy from
non-proteins affects changes in height and weight. Panel C in Table 4 and Fig. 3A show
that for Guatemala, in nearly all cases (98%) the estimated coefficient is insignificant
in the height model. For the weight production function (Panel D of Table 4 and Fig. 3B),
the point estimates are never significant.

<hs>  Philippines</hs>
  ~~~~~~~~~~~

Table 5 shows the distribution of the total energy coefficient estimates for the
Philippines and Fig. 1A and B the corresponding coefficients and confidence intervals for
specifications with CD > 1. As in Guatemala, positive relations are most evident for
specifications with relatively stronger and more exogenous instruments. The positive
impacts of total energy on height and weight are consistent with those found under
somewhat stronger identification assumptions and using the same data, by Liu et al. (2009)
and de Cao (2015). Across all specifications summarized in the Panel A of Table 5, 13%
have positive and significant coefficient estimates (p < 0.05), while none have negative
and statistically significant estimates. Restricting results to the 45 specifications with
HJ test P-values > 0.05 and CD > 7, 64% of estimated total energy coefficients are
positive and significant. Specifications with higher CD statistics tend to have more
concentrated coefficient estimate distributions. If daily energy intake increases by 300
kcal the predicted change in height is 0.18 cm. For weight, evidence is similar regarding
the role of total energy. The bottom panel of Table 5 indicates that for 15% of all the
specifications in the Philippines, the estimated coefficient on total energy is positive
and significant and never negative and significant. Specifications with the highest CD
statistics tend to have larger shares of positive and significant coefficient estimates.
Our median prediction results in a predicted change in weight of 37 g. Panel A of Table 6
(and Fig. 2A) shows that for 39% of all specifications, protein coefficient estimates are
positive and significant. While there are fewer specifications with strong instruments
than in Guatemala, for specifications with CD > 3, 100% of the coefficient estimates are
positive and significant. In specifications with stronger instruments, the estimated
coefficients dispersion decreases. Increasing protein consumption by 10 g per day is
predicted to result in a 2.24 cm change in height. For all specifications (Panel B of
Table 6 and Fig. 2B), 48% of estimated coefficients on protein for weight are positive and
significant – 100% in specifications with CD > 3. Similar to Guatemala, coefficient
estimate dispersion decreases with stronger instruments. Increasing protein consumption by
10 g per day results in a predicted 703 g change in weight. Somewhat surprisingly, non-
protein intakes are generally negatively related to both height and weight gain. For
height, Panel C of Table 6 reports that 88% of the specifications with the strongest
instruments (CD > 3) yield negative and significant estimated coefficients. For weight,
100% of estimates in specifications with the strongest instruments are negative and
significant. These findings for non-protein energy for the Philippines are somewhat
counter-intuitive, because they suggest that such energy intakes are detrimental to
growth. Most individual foods (including those consumed in these regions during the study
periods), however, include both proteins and non-proteins and virtually all diets do.
Consequently, it is unlikely that actual intakes would change in a fashion that increased
energy from non-proteins while simultaneously holding proteins constant. Since Filipino
children's diets included both intakes, on net any negative effects of other macronutrient
sources would have been partly or fully offset by protein effects. For example, not
including breastmilk, at age 6 months, 93% of children had some protein consumption and
from ages 14 to 24 months, all did. Moreover, at age 6 months 75% of children are
breastfed, which also provides protein intakes. In Section 4.5, we show that the model
predicts that a dietary change (relatively rich in proteins but with some energy from
other sources) indeed has positive effects on height and weight, despite negative
coefficient estimates on non-proteins. There are several potential explanations for the
finding that non-proteins are less robustly related to anthropometrics than proteins.
First, it is possible that energy from macronutrients other than proteins do not affect
height and weight, at least aggregating the other macronutrients as we do. Second, it may
be that non-linearities are not captured. For instance, it could happen that carbohydrates
and fat need some proteins to have an effect on anthropometrics—if protein intakes are
zero or very low, other intakes would not affect height and weight. Third, dietary changes
after children stop breastfeeding can result in poorer quality diets, especially poor
quality of carbohydrates and low micronutrient density, weakening any potential link to
anthropometrics. Fourth, the available instruments simply may not be powerful enough to
detect effects of other macronutrients; protein and non-protein intakes are highly
correlated (even before instrumentation), making it difficult econometrically to identify
their distinct effects; in that sense, Guatemala greatly benefits from the experimental
Atole intervention, which provides a clear and strong exogenous variation for protein,
though it is less powerful for other macronutrients.

<hs>  Effects of other inputs and controls</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In addition to the different nutrition intakes, our analysis provides estimates of the
coefficients on lagged height, lagged weight, breastfeeding, and diarrhea. The results
clearly indicate some catch-up height and weight growth. The lagged height coefficient is
consistently negative and mostly significant in the change-in-height equation, indicating
that shorter children at the end of one period tend to grow more in the next period.
Similarly, the lagged weight coefficient is consistently negative and mostly significant
in the weight equation so that lighter children at the end of one period gain more weight
in the following period. With the caveat that the estimates for breastfeeding and diarrhea
are potentially biased due to endogeneity, our coefficient estimates for number of days
without diarrhea are consistently positive and significant for weight in both samples,
suggesting that diarrhea has detrimental effects on weight gain as generally found in the
literature. The coefficient estimates for breastfeeding are positive and mostly
significant for Guatemala. In the Philippines, the coefficient estimates generally show a
positive association between breastfeeding and height while the associations between
breastfeeding and weight show no consistent pattern, similar to findings from Adair and
Popkin (1996).21

<hs>  Counterfactual exercise: increasing nutritional intakes</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We next simulate the full effects of additional protein and non-protein intakes on child
height and weight for the Philippines, complementing the simpler median predictions we
used when interpreting individual coefficients. From the set of specifications with HJ
P-values > 0.05, we select the specification with the highest CD. The simulation is based
on adding one egg per week to a child's diet, assuming no other changes in diet and no
change in diarrhea. Eggs are good for such simulations. They were widely available in the
localities where these studies are situated and are easily consumed by infants. They not
only contain highly bioavailable protein, but also contain energy from other
macronutrients, similar to many other naturally protein-rich foods. A medium (44 g), whole
raw egg contains on average 5.5 g of protein and 40.9 calories from non-protein.22,23
Based on our parameter estimates, a child who consumed an additional egg per week on top
of existing diet, for 18 months – from 6 to 24 months of age – would gain an additional
0.72 cm in height and 265 grams in weight.

<h>CONCLUSIONS</h>
-----------

Arimond and Ruel (2004) described associations between children's dietary diversity and
their height. We build on their insights, examining effects of diet and particularly diet
composition on height and weight growth for children between ages 6 and 24 months, giving
special attention to differences between diets rich and poor in proteins. We improve upon
previous literature by making weaker identifying assumptions, considering two important
anthropometric measures—height and weight, investigating the robustness of our results to
the use of a number of different instruments, and separately investigating the effects of
energy from proteins and from non-proteins while controlling for breastfeeding and
diarrhea. We take advantage of two rich databases, one for Guatemala and the other for the
Philippines, which have longitudinal information on height, weight, and protein and energy
intakes with high frequencies of observations. IV estimation strategies are used to
overcome endogeneity and measurement error problems, using food prices and, in the case of
Guatemala, a randomized nutritional intervention, as instruments. Because there are many
instruments and instrument combinations available, we present results that comprehensively
summarize these combinations rather than selecting only a single set of instruments. Our
findings indicate that increasing energy intake increases both height and weight in both
countries. But the source of that energy, protein versus non-protein, matters. In these
poor populations characterized by high levels of chronic undernutrition, increases in
protein intake drive increases in child height and weight. These results provide evidence
on an important puzzle in the literature while pointing to possible modifications to
interventions designed to improve children's nutritional status. A systematic review by
Manley et al. (2013) using meta-analysis techniques shows that while the average impact of
income transfers from social protection programs on height-for-age is positive, effect
sizes are small and not statistically significant. If households use these transfers
largely to increase the quantity of calories consumed, if the increases in protein
consumption is small in magnitude, or if these proteins are not allocated to children,
then our results suggest that such transfers will have little impact on child
height—precisely what Manley et al. (2013) find. Headey and Hoddinott (2015) examine
impacts of Green Revolution-induced increases in rice productivity on children's
anthropometric status. They find no impact of these on child height, results also
consistent with what we observe here. Our findings, in conjunction with these other
studies, suggest that interventions designed to increase household incomes may only
improve children's nutritional status when they are linked to mechanisms that also improve
the quality of children's diets. Such interventions, e.g., linking nutritional behavior
change communication to social protection interventions or “nutrition-sensitive
agriculture” await further study.

<h>FUNDING</h>
-------

The authors thank Grand Challenges Canada (Grant 0072-03), Bill and Melinda Gates
Foundation (Global Health Grant OPP1032713), and the Eunice Shriver Kennedy National
Institute of Child Health and Development (Grant R01 HD070993) for Financial Support. The
funders have no involvement in the analysis and interpretation of the data, writing of the
paper, or the decision to submit the paper for publication.

<h>CONFLICT OF INTEREST</h>
--------------------

There are no conflicts of interest.


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<ART>Economic development, urbanization, technological change and overweight: What do we learn from 244 Demographic and Health Surveys?
================================================================================

Authors: Yevgeniy Goryakin, Marc Suhrcke
DOI: 10.1016/j.ehb.2013.11.003
Year: 2014  |  Pages: 109-127
ASJC codes: 2001
Keywords: Developing countries, Economic development, Overweight, Socioeconomic factors

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Obesity and overweight are spreading fast in developing countries, and have reached world record levels in some of them. Capturing the size, patterns and trends of the problem has, however, been severely hampered by the lack of comparable data in low and middle income countries. We seek to begin to fill this gap by testing several hypotheses on the determinants/correlates of overweight among women, related to the influence of economic and technological development. We undertake econometric analysis of nationally representative data on about 878,000 women aged 15-49 from 244 Demographic and Health Surveys (DHS) for 56 countries over the years 1991-2009. Our findings support most previously expressed hypotheses of what might explain obesity patterns in developing countries, but they also reject some prior notions and add considerable nuance to the emerging pattern. © 2014 The Authors.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Obesity has become a global phenomenon not solely confined to rich countries (James, 2008;
Popkin, 2007), with the total number of overweight and obese people being estimated at
about 1.5 billion in 2008 worldwide (Popkin et al., 2012). However, the accurate
description of its size, trends and socioeconomic patterns has been compromised by the
scarcity of globally comparable data. One recent study (Finucane et al., 2011) attempted
to fill this void by estimating data on mean body mass index (BMI) among adults over the
age of 20 living in 199 countries (analyzing 960 country years worth of data on 9.1
million participants). They found that between 1980 and 2008, mean BMI in all countries
combined increased by 0.4 (0.5) kg/m2 per decade for men (women). In order to study the
trends and determinants of obesity and overweight specifically in the developing
countries, a small set of recent studies (Martorell et al., 2000; Mendez et al., 2005;
Mendez and Popkin, 2004; Monteiro et al., 2004; Subramanian et al., 2011) has used data
from the Demographic and Health Surveys (DHS), a particularly rich source of information
that had hitherto primarily been used for the analysis of fertility and “traditional”
developing country disease challenges in the area of maternal and child health. In this
article we exploit to an even greater extent the DHS dataset, using data on almost one
million women aged 15–49 from 244 Demographic and Health Surveys (DHS) for 56 countries
over the years 1991–2009. We use this data to examine a broader range of questions than
the previous studies that predominantly focused on how overweight, obesity or BMI in women
varied between socioeconomic groups within a cross section of developing countries. By
combining the DHS data with appropriate socioeconomic indicators or determinants from
other sources, we are in a position to test selected hypotheses that are either derived
from theoretical predictions or, for the most part, have been proposed in the literature
(or expressed in the public debate) without yet having been submitted to closer empirical
scrutiny. Taken together, our findings aim to produce a set of empirically confirmed
stylized facts on patterns, trends and correlates of being above normal weight (defined as
having the Body Mass Index (BMI) of 25, or greater), in the developing countries. As a
number of potential explanations for increasing overweight prevalence have been suggested
over the last years (e.g. see Popkin et al., 2012 for a recent overview), we grouped them
into two main categories (necessarily omitting some well-known potential correlates
related to early life events, e.g. famine (Popkin et al., 2012), as well as genetics-
related explanations): (1) those that concern the relationship between proxies of economic
development and individual overweight, and (2) those examining the association between
proxies of urbanization and proxies of technological change on one hand and individual
overweight status on the other hand. It is important to note that we apply a somewhat more
general definition of “technological change” here than in the economic growth literature,
where it is more narrowly understood as a change in total factor productivity. We broadly
interpret technological change as the process of invention, innovation and diffusion of
various technologies (e.g. labour saving and food production ones) that may facilitate
changes in energy expenditure or consumption, and therefore may affect the likelihood of
being overweight or obese. There is a significant public health and economic literature
which considers the term “technological change” in this similar, broader sense (e.g.
Finkelstein et al., 2005; Huffman and Rizov, 2007; Lakdawalla and Philipson, 2009;
Philipson, 2001; Philipson and Posner, 2003a; Swinburn et al., 2011) Given the data
constraints, we focus the empirical tests of the hypotheses on women only. We examine a
third group of hypotheses, linking overweight prevalence to globalization-related
determinants in a companion paper (Goryakin and Suhrcke, 2013).

<hs>  The role of economic development in overweight</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Overweight is a “disease of affluence”, but only up to a point: as countries grow out of
extreme poverty, overweight among women will increase. However, as countries continue to
grow richer, the increase should slow down at some level of per capita income. Why should
overweight be positively related to national income? The concept of the nutrition
transition (Popkin, 2001; Popkin et al., 2012) emphasizes the role played by increased
affordability of processed foods, as well as foods rich in calories high in fat and sugar
(both due to rising incomes, and advances in food technologies) in developing countries,
especially since the 1970s. Similarly, economic theory (Philipson and Posner, 2003b)
predicts that technological change (which drives and accompanies rising national income)
entails lower costs of consuming calories and higher opportunity cost of expending them,
which, taken together, increases weight. Within this theory, the nonlinearity can arise
because greater income would also increase the demand for health (and thus a BMI closer to
the medically ideal level), assuming that health is a normal good (Grossman, 1972). The
theory predicts that the latter effect would at some point more than compensate the
weight-enhancing effect resulting from the changes in calorie consumption and expenditure.
An adverse economic shock (recession) will be associated with lower likelihood of being
overweight among women. How might body weight respond to a sudden fall in income? It is
tempting to infer from the hypothesized concave and positive relationship between per
capita gross domestic product (GDP) and overweight prevalence from Hypothesis 1.1 that a
recession should be associated with a reduction in overweight in countries below a certain
threshold of per capita GDP and either no change or even an increase in overweight in
middle income countries. However, the concave relationship at one point in time across
countries (which was the focus of Hypothesis 1.1) is more likely to describe a long-term
association. Relationships between short-term changes in per capita GDP and changes in
overweight may well differ from the long-term relationship in levels. In a series of
papers, Ruhm (2000, 2001, 2003, 2005, 2007) examined the impact of recession on health in
a range of high income countries, finding evidence for improving (deteriorating) health in
response to a recession (boom). Ruhm (2000) found that obesity declined in times of rising
national unemployment rates in the US, likely due to (1) the opportunity cost of exercise
falling as unemployment increases, (2) more time available for health enhancing
activities, and (3) possibly due to less income being available for calorie consumption.
In addition, a number of studies have shown that undernutrition prevalence increased
rapidly during times of global economic crises in Cambodia, Bangladesh, Indonesia, Kenya
and Mauritania (SCN, 2009). Similarly, Pongou et al. (2006) have found that child
undernutrition increased considerably during times of economic crises and structural
adjustment programmes in the 1990s in Cameroon. To the extent that undernutrition is the
flipside of overweight, this should mean that overweight will decrease in low income
countries experiencing a recession. In low income countries, women of higher socioeconomic
status (SES) will be more likely to be overweight than those with lower SES, whereas in
middle income countries, the burden of overweight will shift towards women of lower SES,
resulting in an insignificant or mildly negative relationship between SES and the
probability of being overweight. The previous hypotheses predicted the association between
national income and overweight prevalence in all population groups. By contrast,
Hypothesis 1.3 considers within-country differences between women of varying socioeconomic
status (SES), proxied by their level of educational attainment. The hypothesis is inspired
by a widely cited study that demonstrated the shifting burden of obesity from the rich to
the poor as countries’ wealth grows (Monteiro et al., 2004), using largely DHS data from
1992 to 2000 for 37 developing countries. Their results suggested that the reversal in the
obesity gradient occurred at a level of GNP per capita of about 2500 US dollars, which was
broadly supported by a recent systematic review (Dinsa et al., 2012). Another recent paper
(Subramanian et al., 2011), that used more data from DHS, an additional SES proxy (i.e.
wealth) and a more detailed analysis, found that in low income countries, the overweight
burden was mostly concentrated among higher SES people, and that the wealth gradient
became less marked only at a level of per capita GDP of about 5500 USD. Moreover, Neuman
et al. (2011) found that the SES gradient in overweight prevalence did not weaken over
time in the low-to middle income countries studied. The theoretical justification for this
hypothesis can be linked to the explanation given in the Hypothesis 1.2: before the
threshold per capita income is reached, the higher SES people will have greater income,
greater demand for calories and therefore greater weight. However, as economic development
progresses, the demand for thinness and health (backed by better access to healthier
lifestyle opportunities) among higher SES women may start to outweigh the demand for
calories faster than among women belonging to lower SES groups (Jones-Smith et al., 2011),
thus leading to the switchover at a certain income level. In addition, some empirical
evidence (Popkin, 2001) suggests that the income elasticity of demand for certain foods
high in fat is higher for people belonging to lower SES classes. If this is indeed the
case, then rising income levels among the poor may lead to greater relative consumption of
unhealthy diets among them, compared to people from upper SES classes.

<hs>  The role of urbanization and technological change in overweight</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our next set of hypotheses reflects the widespread notion that urbanization and
technological change have been driving the rise in overweight and obesity. Previous
studies have linked urbanization with various technologies potentially associated either
with the reduction in energy expenditure over time (Monda et al., 2007; Popkin, 1999;
Rivera et al., 2002; Swinburn et al., 2011), or with more abundant supply and consumption
of cheaper, energy dense foods (Drewnowski and Popkin, 1997; Popkin, 1999; Popkin and
Gordon-Larsen, 2004). Therefore, we have subsumed several hypotheses concerning the role
of urbanization and different manifestations of technological change under the same group
of hypotheses. Living in urban areas will be associated with higher probability of being
overweight among women. The strong positive association between urbanization and obesity
has been examined and confirmed quite extensively in previous research (e.g. Martorell et
al., 2000; Mendez et al., 2005; Mendez and Popkin, 2004; Subramanian et al., 2011),
although Neuman et al.’s recent paper (2013) suggests that the association between urban
residence and excess BMI may be mediated by higher SES of urban residents. The novelty of
our approach is in the use of a much larger set of individual-level data collected in 56
countries, and in the non-parametric approach used to examine the effect of living in
urban areas on overweight, by taking into account the level of economic development across
countries. In general, living in urban areas can increase the odds of being overweight for
a number of reasons. For example, people living in cities may expend less energy than
those living in rural areas, possibly because they have fewer opportunities to exercise,
because they prefer to spend more time doing leisure activities (such as TV watching) at
home, or because they work in less physically demanding occupations. In addition, those
who live in the cities may transition faster to the so-called “Western” diets rich in
calories from fats and refined carbohydrates, but relatively poor in calories from fruit,
vegetables and cereals (Popkin, 2001; Popkin et al., 2012). This may occur for a variety
of reasons, including greater exposure to food processing technologies, as well as
marketing and distribution systems that promote fast and processed foods consumption.
Next, we consider specific ways in which urbanization can affect the likelihood of being
overweight: Possession of assets that facilitate sedentary behaviour will be associated
with greater overweight prevalence among women Technological change has given rise to an
environment that may make it harder (and thus more costly) to spend calories, with cars
and TVs being but two very widespread manifestations thereof. We hypothesize that owning a
car or a TV set will be related to greater risk of being overweight. The explanation is
intuitive: having a car may predispose people to walk less frequently, and therefore spend
less energy (Sassi, 2010). Previous research has demonstrated that owning a motorized
vehicle was strongly correlated with the probability of being obese in China (Bell et al.,
2002). Similarly, people who own a TV set are expected to be less likely to exercise and,
hence, less likely to “spend” their calories. They may also consume more energy-dense food
while watching TV (Roemling and Qaim, 2012). We will separately also consider if there is
a relationship between frequency of TV viewing and overweight risk. TV viewing may expose
people to mass advertising of certain foods that may encourage people to snack excessively
and may thereby contribute to weight gain (Finkelstein et al., 2005). Some empirical work
in this area (mostly confined to higher income countries) has largely focused on
individual measures of exposure to TV (e.g. number of hours per day watching TV, measured
by self-completed diaries, e.g. (Cutler et al., 2003), or possession of a TV (Roemling and
Qaim, 2012)). Overall, this evidence suggests a rather limited role played by TV exposure,
at least in the high income countries studied (Finkelstein et al., 2005), although
Roemling and Qaim (2012) did find that owning a TV was related to a small but significant
increase in BMI in Indonesia. Note that our goal here is to try and isolate the
overweight-enhancing influence of owning a car and a TV set, rather than the effect of
socioeconomic status and income, which can also be correlated with owning a TV. Our
dataset will allow us to control for both per capita national income as well as for
individual socioeconomic status. In addition, technological change and urbanization are
often hypothesized to lead to increased supply and, hence, consumption of higher energy
and fat density foods (Popkin, 1999, 2006, 2007). Our data will allow us to test the
following related hypothesis: A greater per capita supply of calories will be associated
with higher overweight probability among women. Some research has argued that an increase
in the consumption of calories played a greater role in the rise in obesity, compared to a
reduction in energy expenditure (Cutler et al., 2003; Finkelstein et al., 2005).
Similarly, proponents of the nutrition transition theory emphasize the role played by the
growing proportion of calories obtained from diets higher in fats and refined
carbohydrates, and not so much the increased calories per se (Popkin, 2001). A recent
prominent study (Swinburn et al., 2011) differentiated roughly between two groups of
global determinants of obesity and overweight: those related to the changes in the built
environment, and those related to changes in the food supply. The authors argued that the
built environment has not changed simultaneously and universally to lead to observed
changes in people's weight around the world; hence, the more important drivers are
attributed to the food system domain (including greater supply of cheap, energy-dense
foods, as well as more advanced distribution and marketing systems to increase people's
access to these foods). Similarly, Cutler et al. (2003) argued that although per capita
energy expenditure in the US decreased from 1.69 and 1.57 kcal/min/kg between 1965 and
1975, it remained fairly steady during the period of fast growing obesity prevalence. On
the other hand, available information on trends in energy intakes in the US suggests that
calorie consumption was significantly higher in 1990s compared to the early 1980s
(Finkelstein et al., 2005). Although changes in food systems encompass much more than
changes in per capita supply of calories (one reason being that the available calorie data
is imperfect, and food supply does not accurately capture the calorie consumption by
people living in these countries), testing if there is country-level association between
per capita calorie availability and probability of being overweight, using data from 56
low and middle income countries, may still be very instructive, as the available evidence
so far has been scarce, and largely confined to high income countries. On a macro level,
limited empirical evidence exists that increased food energy supply was positively
correlated with greater weight in USA and UK (Swinburn et al., 2011). On a micro level, a
systematic review of several experimental as well as large prospective cohort studies
concluded that there is strong evidence on the link between fast food consumption and
increasing weight (Rosenheck, 2008). One study which examined the association between
caloric intake and weight in a middle income country (Russia) concluded that the
relationship was strong and positive (Huffman and Rizov, 2007). By contrast, comparing
trends in obesity and diet patterns in the US population, other research found a counter-
intuitive coincidence of decreasing calorie consumption and growing obesity, which was
tentatively attributed to even greater reductions in energy expenditures resulting from
physical inactivity (Heini and Weinsier, 1997). Technological change has also entailed a
shift in the employment of people from agriculture and industry to the service sector,
which in turn may have led to the reduction in energy expenditure: Working in the service
sector is associated with a greater likelihood of being overweight among women. This may
be the case because working in the service industry is – on average – less physically
taxing than manual labour in agriculture. However, the existing empirical evidence is far
from unambiguous. Thus, as Finkelstein et al. (2005) noted, it is true that in the US, for
example, the proportion of workers employed in the manufacturing industries fell from 27%
in 1980 to 19% in 2000, and that the proportion of obese men has almost doubled over this
period. However, the proportion employed in manufacturing was considerably higher in 1960,
i.e. 35%, and yet the proportion of men who were obese changed little between 1960 and
1980. Hence, a more fine-grained analysis, using individual-level data, is needed. We will
test this hypothesis with individual-level indicators on the occupational status of women
contained in the DHS dataset.

<hs>  Data</hs>
  ~~~~

The data in this study comes from several sources: the Demographic and Health Surveys
(DHS), World Development Indicators (WDI),1 the Cross-National Time-Series Data Archive
(CNTS)2 and FAOSTAT.3 The main source is the DHS: nationally representative, population
based surveys, which collect extensive information in the areas of population, health and
nutrition. DHS surveys are extensively described elsewhere (Corsi et al., 2012b;
Subramanian et al., 2011). The WDI, CNTS and FAOSTAT datasets provide a range of relevant
country-level economic indicators that we employed for our hypothesis-testing. The
individual-level DHS data used in this paper covers 19 years (1991–2009) over 56
countries. In the regression analysis, all country-level variables were taken from WDI,
CNTS and FAOSTAT datasets, and merged with individual-level DHS data for respective
countries and years. More information on the data sources used is provided in Appendix. As
the full data was only available on women aged 15–49, we necessarily had to restrict our
analysis to this group. The main outcome variable of interest is being above normal weight
(or overweight, for short), defined as BMI greater or equal to 25 kg/m2. In order to trim
outliers, observations for women whose BMI exceeded 50, or were less than 13, or whose
weight was either greater than or equal to 220 kg, or less than or equal to 20 kg, were
dropped. In addition, observations for women whose height was recorded as either greater
than or equal to 2.2 m, or less than or equal to 0.9 m, were also dropped. We restricted
the sample to women who were non-pregnant at the time of the interview (about 7.9% of
surveyed women aged 15–49 were pregnant). In all countries, information was collected on
women of child-bearing age, and thus included those who had never had children. The
proportion of women with no children (which included women with and without pregnancies at
the time of the interview) varied from about 7–8% of the sample (e.g. in Egypt) to about
45% (e.g. in Morocco), and this difference was largely due to the age structure of the
surveyed population. Thus, in Egypt, only about 8% of surveyed women were under the age of
20 in 1995, while in Morocco in 2003, about 28% of surveyed women were under 20. This
issue may be important for the comparison of overweight prevalence rates across countries,
but we take care of it by adjusting estimates by sampling weights provided with the DHS
surveys. Overall, in the pooled sample, data on BMI was available for about 72% of the
full sample of 1,225,808 non-pregnant women. Again, there was some variation across
countries in terms of the proportion of non-pregnant women with available BMI data (from
99% in Uzbekistan, to only 26% in Brazil), that we account for when estimating country-
specific overweight prevalence by employing sampling weights. In our analysis we used
education as the main socioeconomic variable of interest. While socioeconomic status can
also be proxied by other variables – e.g. wealth, as was done by Subramanian et al. (2011)
– we preferred education, because the way it is defined in the DHS set (using six
educational quartiles, ranging from incomplete primary school to higher education), it may
be considered reasonably comparable across countries as a proxy for the absolute level of
socioeconomic status. By contrast, wealth – as it is commonly constructed on the basis of
DHS data – is a relative measure of SES specific for each country, and thus is harder to
compare when all countries with different income levels are pooled together. Nevertheless,
we also tested the robustness of our findings to the inclusion of an alternative wealth
measure (i.e. car ownership) as education may not fully capture the income and wealth-
related aspects of socioeconomic status. Education was defined using DHS dummies for six
levels: people with no, incomplete primary, complete primary, incomplete secondary,
complete secondary, and higher education. For the graphical analysis (e.g. Fig. 4), we
divided education into four levels: (1) no education, (2) incomplete primary and complete
primary, (3) incomplete secondary and (4) complete secondary and higher education. We then
compared levels 1 and 4. Note that this gradation is different from the one used in some
earlier papers (e.g. Monteiro et al., 2004), which defined top and bottom educational
quartiles by the number of years of schooling in each country. We decided not to follow
their approach in order to avoid dealing with countries for which too many observations
were clustered around a certain value (e.g. zero years of education). In such cases, it
may not be possible to clearly define four separate quartiles, and one would only be able
to deal with three (or even two) groups (Monteiro et al., 2004). In our approach, the rule
for selecting top and bottom “quartile” will apply equally to all countries. A country was
defined as being in economic recession if the country's GDP per capita (in purchasing
power parities [PPP], constant international $, 2005) decreased by 1% or more between
adjacent years. We also checked the robustness of the results by defining a shock as a
more severe economic contraction, i.e. a 5% reduction in GDP per capita year-on-year.
Information on the working status for a woman was based on self-reports, and we captured
service sector employment using an occupational status dummy. Specifically, occupations
were first aggregated into three groups as follows: (1) unemployed; (2) services
(professional and managerial; clerical; sales; household and domestic; services); (3)
agriculture (agriculture employed and self-employed); (4) manual (skilled manual;
unskilled manual). Furthermore, for the services group a dummy was assigned with a value
of one, while for manual and agriculture occupations the assigned value was zero. The
availability of cars and TV sets was measured by individual-level indicators on the
ownership of these items. The hypothesis on the supply of calories was tested using
country-level data on average food supply (kcal per capita per day) derived from FAO
balance sheets. Table A1 in the Appendix describes all the variables used in this paper.
In the regression analysis, we were interested in the association between several
potential correlates and the composite category of “being above normal weight”. We
therefore assigned a value of one to people whose BMI was greater than or equal to 25, and
a value of zero to people whose BMI was less than 25. We also considered including the
continuous variable BMI as the outcome variable, as was done in a recent paper by
Subramanian et al. (2011). However, a change in BMI may have very different implications,
depending on the initial value in its distribution. For example, the change in BMI from 18
to 19 (i.e. from being malnourished to having normal weight – a desirable outcome) has
very different implication compared to an increase in BMI from 24 to 25 (i.e. from having
normal weight to being overweight – an undesirable outcome). Measuring the association
between covariates and BMI would not capture this difference, while measuring the effect
of covariates on overweight (treated as a dummy variable) does. Most hypotheses require
either splitting the sample, or introducing an interaction term to distinguish between
low- and middle-income countries. In this analysis, we used the World Bank year-specific
thresholds defining the split between low income and middle income countries. We then
either split the sample between these two groups and ran the regression analyses
separately, or we introduced an interaction term between the World Bank income level and
the main independent variable of interest.

<hs>  Econometric specifications</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~

The estimates also allow controlling for time-invariant country-specific effects αc. For
example, a country may have a certain endowment of human or natural resources that
contributes to changes in the prevalence of being overweight, as well as to variation in
some of the observed determinants included in the model. Not controlling for such factors
may contribute to a bias in the estimated parameters. Note that this model will allow
parameter estimation only when the main variables of interest are either individual-level
ones or are country-level variables that vary over time. In addition, including time
dummies Dt will allow us to control for other potential time dependence or for any world-
wide factors (e.g. global economic crises) that could affect our associations of interest.
As we are interested not only in the estimation of the main parameters of interest, but
also in whether they are statistically significantly different in low and middle income
countries, ideally we would have preferred to use specifications (2.1) or (2.2) only.
However, as we have six separate educational categories, and our goal was to take
advantage of the whole educational distribution, interacting each educational category
separately with the medium income dummy would not produce very intuitively interpretable
results. Therefore, we split the sample to estimate the association of education with
overweight separately in low and medium income countries, as per specification (1). As we
also had to control for urban residence and GDP per capita in such models anyway, we
presented the results for these three hypotheses using the same specification (1).

<h>RESULTS</h>
-------

In order to put the obesity “epidemic” in developing countries into perspective and
evaluate its comparative severity, it may be informative to start by comparing what
developing countries have recently been experiencing with what today's high income
countries had experienced at earlier stages of the obesity epidemic. Although some recent
studies have looked at the long-term trends in obesity and overweight prevalence in the US
(e.g. Finkelstein et al., 2005; Flegal et al., 1998), there was so far no attempt to
compare these trends with those observed in low and middle income countries from different
regions. Fig. 1 compares the trends in the prevalence of female obesity between a
prominent high-income country (USA) and the four regions that we have defined. The US data
for women was taken from Flegal et al. (1998) and CDC (2010), while the prevalence data
for the developing countries was estimated from DHS data. Please note that in this one
instance, we consider the prevalence of being obese rather than above normal weight, to
ensure comparability between the DHS data with that from the US. Specifically, for each
multi-year period, we constructed a region-specific prevalence of the indicator of
interest, averaging over countries belonging to the respective regions, and using each
country's population as a weight. We describe the regional split in more detail in the
Appendix, Table A2. Although the trends presented in Fig. 1 do not represent a formal
econometric test and therefore are only indicative, they do paint an interesting picture:
the Middle East appears as by far the most worrying region in terms of obesity trends.
Back in 1960, the USA already had reached a considerably higher GDP per capita than the
Middle East has in 2009, and yet it still lagged behind the Middle East for most of the
observed period in terms of female obesity prevalence. Hence one may conclude that the
obesity challenge faced by this region does substantially exceed what even the US has had
to confront. Given that the Middle East still has a lower per capita income than the US
did in the 1960s, further economic development is likely to pose considerable public
health challenges in this region. The comparison to the other regions is more problematic
in that they are at even lower per capita incomes than the Middle East countries on
average and thus the US obesity data would have to go back even further in time to allow
for a meaningful comparison.

<hs>  The role of economic development in overweight</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The results of our first set of more formally tested hypotheses – the role of economic
development in overweight – are reported below: Overweight is a disease of affluence – up
to a point? (cross-country perspective) A simple graphical illustration can be used as an
initial exploration of Hypothesis 1.1. In Fig. 2, we fitted a lowess plot for the
relationship between the country-level proportion of women above normal weight (i.e.
having BMI greater or equal than 25), and GDP per capita, measured using PPP. This very
simple analysis suggests that, indeed, the association between these two variables of
interest is positive and stronger in low-income countries than in the middle-income ones.
As Fig. 2 shows a very simple relationship between the level of economic development and
overweight prevalence, without controlling for any socioeconomic or political factors
(likely to vary widely between countries), this finding should not be over-interpreted.
Nevertheless, the observed pattern confirms earlier findings derived from smaller samples
of countries and individuals (Monteiro et al., 2004; Martorell et al., 2000; Ezzati et
al., 2005; Egger et al., 2012). A few interesting cases are worth highlighting: in 2007
Egypt had a far greater female overweight prevalence than could be predicted from their
per capita GDP level. On the other hand, another African country – Namibia – was in the
reverse situation, being located below the regression line. The high prevalence of obesity
in Egypt relative to its GDP level was discussed in other studies (e.g. Martorell et al.,
2000). Future research should try to identify the factors that help account for these
large differentials. In Fig. 3, we examine how the same relationship may have evolved over
time. It emerges that the peak at which the prevalence of being overweight is reached is
at approximately USD 5000–6000 per capita, PPP. Moreover, it appears that this peak level
has been slightly shifting to the left over time, suggesting the existence of a learning
process, which allows countries that reach higher income levels to switch to a descending
trajectory for overweight in the following time periods. On the other hand, it is quite
worrying that for a given level of economic development, the prevalence of overweight
tends to increase over time. Thus, at USD 5000 GDP per capita, the prevalence of being
above normal weight among women in 1991–1994 was approximately 35%. In 2003–2009, this
proportion increased to almost 50%. A similar upward shift of the income-BMI curve over
time was observed in another study, using US data (Ezzati et al., 2005). This patterning
emphasizes once again the role played by determinants of overweight other than national
income, the influence of which was apparently increasing over time. It is also worth
noting that this reflects the reverse picture of Preston Curve (Preston, 1975) which
indicates an improvement in life expectancy over the decades (attributed to technological
change), while in the case of overweight we observe a deterioration. Given the trends
mentioned in a previous paragraph, it appears that as time passes, countries may learn to
switch to a downward trajectory faster (i.e. at lower level of GDP), but before doing so
they tend to reach a greater overweight prevalence than previously. A more formal test of
this hypothesis can be performed with the help of simple regression analysis as outlined
in equation 1 above, using individual-level overweight status as an outcome variable. In
Table 1, column 1, we see that the log of GDP per capita generally has a positive
association with the probability of being overweight, suggesting that a 10% increase in
GDP per capita is associated with about 1.2 percentage points (p.p.) higher probability of
a woman living in that country being overweight. Put differently, a twofold increase in a
country's GDP from, say, 500 to 1000 USD, is predicted to lead to about 12 p.p. higher
probability of being overweight. This finding is robust to including country-level fixed
effects as outlined in column 2 (although the magnitude of the effect becomes smaller).
This is a relatively small effect, but note that it is averaged over all regions and
years, and is derived after controlling for educational attainment and for the proportion
of people living in urban areas. By contrast, results in columns 3 and 4 (as well as in 5
and 6) show that the estimate of the association between log GDP and the probability of
being overweight among women is insignificant for the sample of low income countries, and
positive and significant for middle income countries. This finding contrasts with the
picture presented in Fig. 2. We will come back to possible explanation for this finding in
the Additional Checks section below. An adverse economic shock (recession) will be
associated with a lower likelihood of being overweight among women. The results for
Hypothesis 1.2 are summarized in columns 1 and 2 of Table 2. The first column provides the
OLS results. We see that economic decline, as measured by a dummy for countries that
experienced a decline of 1% or more in their real per capita GDP compared to the previous
year, is associated with an increase in the probability of being overweight in low income
countries, and a decrease in the likelihood of being overweight in middle income
countries. This finding is, however, not robust to including country-level fixed effects
(see column 2): the fixed effects results show that with economic decline people in poor
countries are less likely to be overweight – as Hypothesis 1.2 predicted – while those
living in richer countries gain weight. Note that when we defined an economic shock
differently, i.e. as a contraction by 5% or more in real GDP per capita, we obtained very
similar results in the model without country fixed effects (CFE), and somewhat different
results for the model with CFE. Specifically, while the interaction parameter was very
similar, the economic shock parameter for low income countries was now positive and
significant (b = 0.03), suggesting that the effect of a more significant economic shock
may operate differently in the lower-income countries. Nevertheless, as only 3% of the DHS
sample lived during years of such strong recessions, it is important to be cautious in
interpreting this specific finding. We can also test more directly how work status of
women is correlated with being overweight. In Table 2, columns 7 and 8 we see that in low
income countries, working is surprisingly negatively correlated with overweight, while the
reverse is true in middle income countries. Our findings thus partly support the previous
evidence of a positive association between country-level recessions and weight reduction
in the low income countries (SCN, 2009). As for the middle income countries, our findings
contradict our hypothesis (and thus the work by Ruhm (2000, 2001, 2003, 2005, 2007)) but
are in line with the small strand of literature arguing that recessions increase the
propensity to be overweight (Morris et al., 1992; Ludwig and Pollack, 2009). One potential
explanation for this finding is that in the more developed countries, economic recessions
(and loss of income from the main breadwinner) may lead to greater employment of women to
supplement family income as a coping mechanism (Lim, 2000). In turn, they may have less
time for cooking and may thus be more likely to be overweight. On the other hand, the
reverse may be true for women living in the less developed countries, who may have to cut
their total consumption of calories altogether (thereby losing weight). Nevertheless,
there is reason to doubt this explanation in that the scope of finding work during
recessions may be quite limited for the previously unemployed women. Instead, it is
possible that the observed increase in overweight among women in recession-hit middle
income countries, and the reverse trend in the low income countries, is due to different
patterns of dietary response. For example, women in poor countries may consume fewer
calories during recessions due to more binding constraints on overall food-related
spending, while women in middle-income countries may have an option to switch to less
healthy, high calorie food instead. Unfortunately, it is not possible to explore this
issue further given the available data. Having said that, the finding that individual
working status is positively associated with overweight and obesity in the middle income
countries, is in line with the literature that argues that being employed may be related
to fewer opportunities for exercise and taking care of one's health, as well as to a line
of reasoning that women who work may be less likely to spend time cooking nutritious food,
thus contributing to the increase in overweight (Finkelstein et al., 2005). In low income
countries, women of higher socioeconomic status (SES) will be more likely to be overweight
than those with lower SES, whereas in middle income countries, the burden of overweight
will shift towards women of lower SES, resulting in an insignificant or mildly negative
relationship between SES and the probability of being overweight. The association between
education and the probability of being overweight is generally positive for the overall
sample (Table 1, columns 1 and 2). Thus, women who have the least education, are about
11p. p. less likely to be overweight than those with the most education. The country fixed
effects specification gives very similar results. Again, this number conceals variation
between low and middle income countries: columns 3 and 4, as well as 5 and 6 in Table 1,
show that at all levels of education, the association between this measure of
socioeconomic status and the probability of being overweight is weaker for the sample of
middle income countries. Moreover, when country-level fixed effects are used, the
relationship between education and probability of being overweight actually turns negative
in middle-income countries, as expected. This finding was affected to only a small extent
by the inclusion of the alternative wealth measure, i.e. car ownership (results not shown
here but available from the authors upon request). Additional evidence on Hypothesis 1.3
is also presented in Fig. 4 below, showing that up until about 5000–6000 USD GDP per
capita (PPP), those in the top education quartile are more likely to be overweight than
those in the bottom quartile. Beyond this threshold, however, it is those with the least
education who have consistently greater probability of being overweight. This association
becomes even more pronounced – and the threshold declines to around 4000 USD – when the
obesity prevalence is measured on the vertical axis (see Fig. A1 in the Appendix). Note
that our finding is consistent with the results of other, smaller-scale studies. For
example, a negative association between education and obesity probability was found for
women living in China (Xuhong et al., 2008), Brazil (Marins et al., 2007), Eastern Europe
(Pikhart et al., 2007), Iran (Hajian-Tilaki and Heidari, 2009), Argentina (Fleischer et
al., 2008) – all countries at a level of around 4000 GDP per capita (PPP, international
2005 $) or higher. In contrast, many earlier studies focussing on less developed countries
tended to find positive associations between education and obesity (Sobal and Stunkard,
1989). In a recent study on the relationship between educational attainment and overweight
among Chinese women (Jones-Smith et al., 2011), no relationship was found using 1989 data,
but a strongly negative relationship (OR = 0.22 (CI 0.11–0.42)) was found for 2006. In
another recent study that used World Health Survey data (Moore et al., 2010), the general
finding was a positive relationship between education and overweight. Note, however, that
their results were not split by country income classification, so it is hard to directly
compare the results to ours. Monteiro et al. (2004) also found that as national income
increased the burden of obesity was shifting from the top to the bottom socioeconomic
status. The fact that our finding is similar, using considerably more data, and using a
different definition for the top and bottom educational attainment, is encouraging.
Similarly, Martorell et al. (2000) found that more educated women living in very poor
countries were more likely to be obese than the least educated ones, while this gradient
disappeared as countries got richer. On the other hand, Subramanian et al. (2011) used
wealth as an additional proxy for socioeconomic status. Their finding was different in
that there was no shift in the burden of obesity from the richest to the poorest people as
national income was increasing (although there was a shift when the richest quartile was
compared to the third and second quartile). That said, those results are not directly
comparable to ours, since they used predicted BMI level, rather than prevalence of being
above normal weight as an outcome variable. They also found that the association between
wealth and BMI was considerably stronger than the association between education and BMI.
However, since including both education and wealth in the same equation may mean that the
influence of one variable is captured in another, it is hard to conclude from this with
certainty that wealth is more important than education for nutritional health.

<hs>  The role of urbanization and technological change in overweight</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In what follows we summarize the results from our four hypotheses that could be subsumed
under the factors capturing indicators of technological change. Living in urban areas will
be associated with higher probability of being overweight among women. The tests of
Hypothesis 2.1 are also contained in Table 1. It is obvious that this hypothesis is
supported by the results from all specifications, suggesting that, in general, living in
urban areas is related to an about 7–12 p.p. greater probability of being overweight, even
after controlling for education. Moreover, the effect of urban residence on overweight is
weaker in countries with a higher level of income – consistent with the finding from
another study (Popkin et al., 2012) which used a different method, and different data –
again suggesting a potential learning curve that occurs in countries as they undergo
economic transformation. Also, Fig. 5 shows that for all levels of GDP per capita, the
probability of being overweight is higher in urban areas, and thus unlike education, there
appears to be no switchover in obesity occurring from urban to rural areas as national
income grows larger. This confirms previous findings by Mendez et al. (2005), which
however where based on less comprehensive data and used a smoothed plot, rather than
lowess regression. Similarly, a recent paper using data from 42 low and middle income
countries (Popkin et al., 2012) also found that on average, urban women had higher
baseline prevalence of being overweight, compared to rural women, and this was true for
all countries they studied. Moreover, they found that in countries with higher GDP per
capita, there was relatively little association between residence and overweight
prevalence, and that this association was much stronger in lower income countries. Given
the worldwide trend towards urbanization that is set to continue in developing countries
(United Nations, 2011), the consistently overweight-enhancing effect of urbanization does
raise concerns that this will remain a factor driving a further spread of obesity in the
developing world. Possession of assets that facilitate sedentary behaviour will be
associated with greater overweight prevalence among women. Hypothesis 2.2 was confirmed
both in OLS specification and CFE specifications (see Table 2). Thus, having one car is
associated with an about 12–14 p.p. higher probability of being overweight. The effect was
also considerably stronger in the low-income countries compared to the middle income ones,
suggesting that changing transportation habits there may entail a particularly high risk
of adverse weight outcomes. Similarly, TV ownership was significantly related to female
overweight in both OLS and fixed effects specification (see Table 2). Interestingly, the
magnitude of association is very similar to what we found for car ownership variable,
suggesting that having a TV is related to an about 12 p.p. greater probability of being
overweight among women in the low income countries. The association becomes slightly
smaller in size in the middle income countries when country fixed effects are included. We
also found a quite strong dose-response relationship between frequency of watching TV and
overweight risk (using the country fixed effects specification – detailed results
available upon request). Thus, compared to the reference group of never watching TV, those
who watched it less than once a week; at least once a week; and almost every day, had an
4.5 p.p., 7.2 p.p. and 11 p.p. greater risk of being overweight, respectively. A greater
per capita supply of calories will be associated with higher overweight probability among
women. The food supply hypothesis was tested by running specifications reported in columns
9–10 of Table 2. As expected, there is a significant positive association between average,
country-level per capita supply of calories (for convenience of interpretation, expressed
in 1000 kcal per capita) and the probability of female overweight in the simple OLS model.
The effect is also stronger in the middle income countries. To put this into perspective,
the average total supply of calories, across all countries, is about 2400 kcal/person/day.
Increasing this availability by 1000 kcal, or by about 41%, would lead to about 11.9 p.p.
greater probability of women being overweight in the middle income countries. The effect
remains significant for the middle income countries in both models. It should be
emphasized that this is a test of the relationship between average per capita supply of
calories and the probability of being overweight, and, as noted above, the former is a
crude measure of the actual consumption of calories in the country. This measure does not
take into account the potential changes in the patterns of the diet either, e.g. the
potential shift to higher consumption of calories from refined carbohydrates and fats
(Popkin et al., 2012). Nevertheless, the size of the association that we found for the
middle income countries supports the hypothesis that greater supply of food plays a role
in increasing overweight risk, at least in the middle income countries. Working in the
service sector is associated with a greater likelihood of being overweight among women.
This hypothesis was also confirmed in both the OLS and fixed effects specification (see
columns 3 and 4 in Table 2). Thus, working in the service sector was associated with an
about 8 p.p. higher probability of being overweight among women, and the effect was
somewhat weaker in the middle income countries (although it still remains significant).

<h>ADDITIONAL CHECKS</h>
-----------------

One potential concern with our findings is that traditionally used BMI cut-off points
ultimately are arbitrary and at least in some countries or regions inappropriate to
capture the prevalence of weight problems (James, 2004, 2008). To tackle this problem, we
ran the same regressions, but with differently defined cut-offs for being overweight. The
results are presented in Fig. 6, focussing – for illustrative purposes – on the role of
education in overweight and its sensitivity to changes in the cut-off. All underlying
regression estimates included the same controls as in Table 1. In the low-income
countries, the effect of education is very sensitive to the cut-offs used. Thus, when
being overweight is defined as having a BMI greater or equal to 23, the people with some
or complete university education have about 15 p.p. greater probability of being
overweight than the reference group. However, this differential falls by more than 50, to
about 9% p.p., when the cut-off is at about 26. The effect of university education on
being overweight and obese is at its smallest when the BMI cut-off is 30. Comparing this
picture to the one emerging for middle income countries (Fig. 6), we can see that there is
much less sensitivity in the effect of education by different BMI cut-offs. We also
checked how sensitive the results were to using different thresholds defining the split
between low and middle income countries. Table 3 shows that the OLS results were
particularly sensitive for the log GDP per capita variable (please note that OLS version
was chosen over country fixed effects, as there was an insufficient number of countries to
estimate parameters for log GDP per capita variables in columns 2 and 4). It is important
to bear in mind that in the results presented in Table 1, the effect of GDP on the
probability of being overweight was surprisingly insignificant in low income countries and
positive in middle income ones. However, now we see that this is only true when
comparatively low income levels are chosen for the threshold separating low from middle
income countries. When the middle income level was defined as having a GDP per capita
greater than 3000 USD or higher (PPP, 2005 international dollars), our earlier unexpected
finding is reversed, and is now in line with the original hypothesis. Note that this
finding is also in line with what we found in Fig. 2. Education turned out as another
category that is quite sensitive to the cut-offs used: the relationship in the predicted
direction was again at its strongest when a higher cut-off was used. There was little
change in the association between urban living and being overweight regardless of the
threshold level chosen. Table 4 provides the same information for the remaining hypotheses
(for convenience, only the main parameter estimates are presented). We see that in this
case the choice of the cut-off had little effect on almost all variables. Hence we
conclude that the choice of a cut-off for the income level made a substantial difference
only for Hypotheses 1.1 and 1.2. Note that in this case again the OLS version was chosen
over country fixed effects, as there was an insufficient number of countries to estimate
several parameters in columns 4 and 5. We also examine whether the effect estimates of the
main determinants vary by region. In Table 5 we present OLS results for the equation
reported in the first two columns of Table 1, but this time split by 4 regions, and for
two different outcomes: being above normal weight (i.e. when BMI is 25 or greater), and
being obese (i.e. when BMI is 30 or greater). Here the OLS version was again chosen
instead of country fixed effects estimates, as there was an insufficient number of
countries to estimate parameters on the log GDP per capita variable for columns 4 and 8.
Several interesting findings emerge. First, in the Americas and the Middle East, education
has a different association with the probability of being overweight among women, than in
Africa and Asia (qualitatively, the same results are obtained when using obesity as the
outcome variable.) While in the Americas and the Middle East, women with the most
education have a lower probability of being overweight than almost all other educational
categories (except the lowest one), this is not the case in other regions, where less
education is generally associated with a lower probability of being overweight. A possible
explanation for this pattern is that most countries in the Americas and Middle East are
already past the GDP threshold at which the overweight burden tends to shift to lower
socioeconomic groups. In addition, log GDP per capita has a considerably stronger
association with overweight in the Middle East: in this region a 10% greater GDP is
associated with an about 12 p.p. higher probability of being overweight. It appears that
in the Middle East, economic development may fuel the rise in overweight prevalence much
faster than in the rest of the world. Also, the association between age and obesity is
much stronger in the Middle East and in the Americas than in other regions (not shown
here). This implies that as the population ages in those regions, the obesity burden there
may become particularly acute.

<h>CONCLUSIONS</h>
-----------

While the growing obesity challenge in the developing world may have been fairly widely
acknowledged by now, precisely capturing the size, patterns, trends and determinants of
overweight and obesity in developing countries has thus far been severely hampered by the
lack of comparable micro data in low and middle income countries. To date, most of the
broadly related studies focussed either on calculating country-specific prevalence of
obesity, or on examining how socioeconomic status of individuals and their place of
residence is related to obesity burden. By taking advantage of a considerably bigger
sample than used in previous studies, we have re-examined previous findings and have
tested a number of additional hypotheses derived from existing theoretical literature, or
from widely held notions about alleged determinants of being overweight, that had been
taken for granted without having been empirically tested. Wherever possible, we tested for
several hypotheses simultaneously, by including relevant variables of interest at the same
time. On the whole, our results confirmed the set of hypotheses about the association
between economic development and overweight: Hypothesis 1.1: The relationship between
national per capita income and obesity is positive and concave; Hypothesis 1.2: In an
economic recession, people in poor countries lose weight and, hence, are less likely to be
overweight (although this was not the case in the middle income countries); Hypothesis
1.3: The relationship between education (as a proxy for socioeconomic status) and the
probability of being overweight is positive in the low income countries and negative in
medium-income countries. The latter finding in particular suggests an important policy
implication: in order to minimize negative consequences of economic development in the
form of greater overweight, there may be reason to target attention at preventing
overweight and obesity among higher socioeconomic groups in low income countries, and at
lower socioeconomic groups – in middle income countries. Moreover, it appears that the
greatest returns to better nutritional status from more education are in the Americas and
the Middle East regions (see Table 5). Given that the Middle East is the most problematic
region in terms of obesity prevalence, this finding is especially promising, as additional
investment into female education in this region is likely to bring the greatest returns in
terms of reducing overweight. The picture emerging from the next set of hypotheses
suggests that urbanization and related technological change do play at least some role in
the growing overweight prevalence: Hypothesis 2.1: Our finding that living in urban areas
is related to significantly higher likelihood of being overweight for countries at all
income levels suggests that the continuous urbanization process taking place in the
developing countries poses a serious public health challenge. Hypothesis 2.2: Both car and
TV ownership are robustly related to overweight outcomes, with the magnitude of the
association being smaller (yet still positive) in the middle income countries compared to
the low income countries. Hypothesis 2.3: Greater per capita calorie intake is positively
related to overweight, but only in the middle income countries. Hypothesis 2.4: Shifting
patterns of employment from agriculture into services, traditionally associated with
urbanization and technological change are also significantly related to a greater
probability of being overweight in both low and middle income countries. In addition, we
have dealt with the previously mentioned cut-off problem (e.g. James, 2004, 2008) in a
systematic way. For example, we have demonstrated that the results can be quite sensitive
to choosing different thresholds for defining overweight. Moreover, we checked how the
estimation results varied depending on the level of income threshold chosen to
differentiate between low and middle income countries. Inevitably, our study suffers from
several limitations. For example, the sample was necessarily restricted to women only,
mostly of child-bearing age. Therefore, generalizing our findings to women of all age
groups, let alone to both genders, is impossible. Nevertheless, since the age group 15–49
represents the most economically active group of women, who also typically have a number
of people depending on them (including children and the elderly), focussing our attention
on this demographic segment seems to cover a sizeable and important share of the
population. Also, by the very nature of the sampling undertaken for the DHS surveys, most
sampled women were mothers with at least one child under 5 years of age (Monteiro et al.,
2004). This can be problematic in that such women may be more likely to be overweight, and
therefore the estimated prevalence of obesity may be slightly overestimated. Nevertheless,
since our goal was not to estimate country-level obesity prevalence, but rather to test
the statistical association between overweight status and its correlates, this should not
be a significant concern in our study. The sample composition was also changing depending
on the availability of certain variables. For example, information on the occupational
status of respondents was available for about 50% of the sample with BMI information,
while for most other variables the data was much more available. In addition, since the
data we used is of a cross-sectional nature, we have to caution against deriving too
strong causal inferences about the identified relationships. Rather, our goal was a more
modest test for any potential partial correlation between a number of relevant
socioeconomic variables and overweight. Finally, we did not explore how variation in
overweight status was partitioned between national and community levels. A recent paper by
Corsi et al. (2012a), using similar data, did focus on this aspect. Despite the
limitations, this study presents an important step towards quantitatively examining the
role that different proxies of economic development, urbanization and technological change
play in explaining overweight in developing countries, using a unique global dataset.
While the findings support several previously expressed hypotheses of what might explain
obesity patterns in developing countries, they also reject some prior notions, and add
considerable nuance to the emerging pattern. More research is needed to assess the extent
to which the findings reflect a true causal relationship.


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<ART>Endogenous versus exogenous money: Does the debate really matter?
=================================================================

Authors: Arkadiusz Sieroń
DOI: 10.1016/j.rie.2019.10.003
Year: 2019  |  Pages: 329-338
ASJC codes: 2002
Keywords: Banks, Central banks, Endogenous money, Exogenous money, Money, Money creation, Money supply

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Whether money is exogenous or endogenous is the subject of one of the most important and intriguing debates in monetary economics. The aim of this article is to contribute to this longstanding debate through detailed examination of different notions of endogeneity and exogeneity of money. I argue that the debate has been too simplified. In reality, money can be either endogenous or exogenous, depending on several factors. Not only has the debate prompted some economists to draw too far-reaching conclusions, but it also misses the point.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Whether money is exogenous or endogenous is the subject of one of the most important and
intriguing debates in the monetary economics. The discussion of whether the money supply
is a cause or an effect of economic activity goes back to the dispute between the Currency
School and the Banking School, if not before (Artesis and Howells, 2001). The neoclassical
synthesis adopted an exogenous-money position, which was challenged, among others, by
Kaldor (1970), Chick (1973), and Moore (1998). Although it is now a consensus position
that central banks set interest rates and allow the quantity of reserves to float, as the
post-Keynesian economists argued, the debate is alive and of key importance for monetary
theory and policy. At the most general level, exogeneity means the supply of money is
independent of demand. Endogeneity means the opposite. On the one hand, it should be clear
that money is endogenous. After all, the majority of money is supplied by commercial banks
in the form of bank deposits. It would be strange to assume that commercial banks do not
respond to the public's demand for loans or preferences regarding the form of money it
wants to hold. On the other hand, it is similarly obvious that money is exogenous. Do not
central banks have a monopoly on cash issuance? It would be rather awkward to assume that
a monopoly producer does not control the supply of its product, as this is the very
definition of a monopolist. In this article, I cut this Gordian knot. To do so, I start by
discussing different notions of monetary endogeneity/exogeneity, as the term may be
understood differently. For example, Palley (2002) lists several different types of money
endogeneity/exogeneity.1 As these notions are often conflated, I analyze them to clarify
the debate. The meanings I distinguish among are shown in Table 1. In the remainder of the
article, I analyze the notions and prove that economists often wrongly color conclusions
about one concept of exogeneity with conclusions about another concept. As one can see in
the table, I differentiate between exogeneity/endogeneity in the following senses: origin
and evolution (Section 2), quantity (Section 3), bank money (Section 4), statistics and
policy (Section 5), and control (Section 6). In Section 7, I discuss the debate between
the horizontalists and the structuralists. Section 8 concludes.

<h>EXOGENOUS/ENDOGENOUS ORIGINS AND EVOLUTION OF MONEY</h>
---------------------------------------------------

The first notion of exogeneity/endogeneity concerns the origins of money. According to
Knapp (1924) and his followers, on the one hand, money was introduced by the authorities.
Money is thus an exogenous creation of law and the state. On the other hand, Menger (1871,
1883, 1892) developed the concept of spontaneous or “organic” genesis of money, which
eventually became the mainstream theory of the origin of money. According to him, money
was not the top-down result of an act of will, but the unplanned product of market
mechanisms. Money evolved spontaneously in the market through the self-interested actions
of individuals who wanted to improve their position. Menger (1871) noted that economizing
individuals are inclined to exchange their products not only for those goods that they
desire to consume directly, but also for more marketable goods, as the possession of goods
with high marketability improves their chances to acquire what they really want. As more
and more people start to accept these goods in their exchanges, their marketability rises
even further. This gradual, self-reinforcing process eventually leads to the selection of
a common medium of exchange—that is, money—although nobody intended it. Hence certain
commodities were endogenously selected as monies on the basis of their ability to reduce
transaction costs and facilitate exchange. The second notion of exogeneity/endogeneity
concerns the evolution of money after its origin—in particular, the switch from commodity
money to fiat money. Mainstream economists believe that money endogenously evolved from
commodity money to fiat money, as individuals economized on production and transaction
costs (for example, Thornton 2000). As it required many more resources to produce
commodity money, society replaced it with cheaper, fiat money. Meanwhile, Austrian
economists argue that fiat money did not endogenously (read: spontaneously) emerge on the
free market, but resulted from exogenous government intervention in the monetary sphere
(for example, Hoppe, 1994; Hülsmann, 2008).

<h>EXOGENOUS/ENDOGENOUS QUANTITY OF MONEY: THE ROLE OF THE MONETARY SYSTEM</h>
-----------------------------------------------------------------------

The origins and evolution and nature of money are one thing, and the quantity of money is
another. The debate about exogeneity/endogeneity of money generally concerns the
determination of the latter. Indeed, for Fontana (2003, 291–92), “the essence of
endogenous money theory is that the stock of money in a country is determined by the
demand for bank credit, and the latter is causally dependent upon the economic variables
that affect the level of output.” Similarly, for Rochon and Rossi (2013, 214), the essence
is that “the supply of money expands and contracts with the needs of production, in
response to expectations of aggregate demand, through the banking system.” However, the
debate over whether the quantity of money is endogenous or exogenous is too general. Our
position depends not only on our understanding of exogeneity/endogeneity, but also on the
monetary system and whether we are analyzing outside or inside money. For example, it is
widely believed that under the gold standard—understood here as a monetary system without
a central bank and government intervention in the monetary sphere, with gold as the
outside money—the money supply is exogenous, as the total stock of gold cannot be
increased at will. Commercial banks have no control over the money supply. In a full-
reserve system, they cannot create money at all, while in a fractional-reserve system,
they need gold reserves, the supply of which cannot be increased at will—that is, the
reserves constitute an exogenous constraint on credit creation. This is the core of the
main argument for and against the gold standard: neither the government nor the banking
system is able to arbitrarily increase the money supply. For supporters of this system, it
protects people against inflation, while for opponents it makes the monetary system not
elastic enough to stimulate the economy during recessions. However, it is not the case
that the supply of gold is a totally independent factor under the gold standard. After
all, the supply of money under the gold standard can only be what is consistent with the
underlying market fundamentals. Indeed, the allocation of gold between monetary and
nonmonetary uses, gold mines’ decisions about the production level, and gold flows between
countries are endogenously determined by the price mechanism operating within the economic
system and the resulting changes in the balance of payments. Hence, if we use “endogenous”
as a synonym for “within the market system,” then money is endogenous under the gold
standard (although the total stock of gold is given exogenously, the supply of gold
flowing into market is, by definition, endogenous, as it depends on unfettered decisions
of market participants). In contrast, under a fiat standard, the supply of money is
exogenous, when the world is understood as being outside the market system, as it is
determined, at least partially, by the central bank, a nonmarket institution. In
principle, under a fiat standard, the central bank, a monopolistic producer, can choose
the supply of outside money to be whatever it wants, but in practice, it can decide to
respond more or less to commercial banks’ demand for reserves, rendering it dependent on
the state of the economy and thus endogenous. Hence, whether money is endogenous or
exogenous depends on the monetary system and its institutional details.

<h>EXOGENOUS/ENDOGENOUS BANK MONEY</h>
-------------------------------

The endogeneity/exogeneity debate often boils down to the debate about the proper theory
of banking, or, to be more specific, the right theory of money creation and bank lending.
According to the exogenous view, banks need reserves in order to grant loans on top of
them. Meanwhile the endogenous view claims that loans create deposits. The confessions of
central banks’ practitioners and the failure of quantitative-easing programs to revive
credit activity and economic growth provide evidence of endogeneity in that sense. Banks
do not lend simply because they have more reserves. Rather than paying attention to the
relationship between commercial and central banks, or between banks’ loans and reserves,
some researchers focus on the relationship between commercial banks and their clients, or
the key role of both in the payment system. The supply of money is considered endogenous
in this view as it is determined by firms’ need to pay for the costs of production. The
production decisions of companies generate the demand for loans (Moore, 1988). Commercial
banks set the interest rate on loans (the policy rate plus a markup) and accommodate the
demand for loans, so money is endogenous. However, commercial banks do not merely respond
to the demand for loans. They can ration credit and alter the borrowing rate and other
credit conditions to affect the demand for loans. This means that although commercial
banks cannot determine the loan supply at will (as they have to find creditworthy
borrowers), they do not merely accommodate the demand for loans. Hence money is not fully
endogenous in this sense. Certain economists believe that money is endogenous by nature.
As Rochon and Rossi (2013, 224) put it, “Money is and has always been an endogenous
phenomenon, owing to its being essentially tied to the nature of debt and the need for a
means of final payment that has to be provided by a third party on the agents’ demand.”
The endogeneity of money does not depend on any institutional factors or the adopted
policy by the central bank; rather, it is a natural occurrence in a capitalist economy,
even a logical necessity.2 This is because money is used in every payment in the economy,
and the payments are elicited by the “needs of trade.” If “endogenous” means here money
that is not just a veil, as the neoclassical economists assume, I agree with this notion.
After all, because of the Cantillon effect, changes in the money supply are not neutral,
even in the long term (Sieroń, 2019). And I concur that money is an inherent feature of
capitalism, although for different reasons (not because it is allegedly elicited by the
need of trade, but because it enables rational economic calculation). However, referring
to its nature is a rather unusual way of framing the debate about the
endogeneity/exogeneity of money. Money, of course, plays a key role in the market economy,
but it does not follow that institutional features of the monetary system do not matter.
Given that the debate about the endogeneity/exogeneity of money often boils down to
whether central banks control the money supply, 3 one cannot abstract from central banks’
policies.

<h>EXOGENOUS/ENDOGENOUS IN THE STATISTICAL AND POLICY SENSES</h>
---------------------------------------------------------

Moore (1988) distinguishes between exogeneity in the statistical and control senses (I
analyze the latter in Section 6). In econometrics, or statistics, exogeneity means a
variable is independent of other variables, while endogeneity implies a variable is
jointly determined with other variables in the system. Of course, in reality all variables
are interrelated.4 Hence, in a statistical sense, whether a variable is exogenous or
endogenous can only be determined in the context of a particular model. We thus say that a
variable is exogenous when its determinants do not include variables determined within the
model, while endogenous variables are those whose values are determined by the model
(Chick, 1973). Now, it should be clear that the debate is not about exogeneity in the
statistical sense, as “it takes little technical expertise to identify exogenous variables
in an explicit model” (Chick, 1973, 85). We all know, for example, that in the quantity
theory of money, the money supply is supposed to be exogenous. It is similarly
uncontroversial that the money-multiplier model assumes the monetary base is exogenous.
These assumptions are what transform tautologies into theories. But what really matters is
the adequacy of the model, not the nature of the variables per se. Hence the debate is not
really about the exogeneity of money, but the determinants of the money supply in the real
world, where the term “exogeneity” does not apply. The confusion stems from the fact that
what really matters is causality, not exogeneity, but only exogenous variables can be
independent sources of change within a particular model. So, if we investigate the impact
of changes in the money supply on prices, it sounds reasonable to assume that the money
supply is exogenous in a particular model, although in reality the money supply can be
affected by other variables. The bewilderment is compounded by the fact that some people
use the term “exogenous” to describe policy changes. The government is seen as being
outside the private sector, so this approach seems to be justified. As a reminder,
exogenous variables are those whose values are determined outside the system under
consideration. Therefore, when economists model the private sector, including its response
to some policy changes, it makes sense to assume that money is exogenous in the policy
sense—that is, that policy parameters are exogenous. However, there are some problems
related to this approach. Although it is true that the government is not subject to the
profit-and-loss mechanism, it cannot fully abstract from developments in the private
sector. Actually, public choice theory shows that the private sector demands certain
policy actions (Tullock, 1993). It is also true that at least some components of the money
supply are provided by the public sector. But we should not on this basis draw the
conclusion that the money supply is exogenous, as in doing so we would be assuming
something that needs to be proven. After all, the majority of the money supply in the
modern monetary system is created by commercial banks in the form of bank deposits (McLeay
et al., 2014a). Even if one agrees that the monetary base is determined exogenously by the
central bank, a nonmarket institution (and not all economists agree with this), it does
not follow that the whole money supply is exogenous. Exogenous variables should not be
conflated with policy-determined variables. After all, monetary policy is set generally in
response to past, current, or expected economic developments (Goodhart, 2001).

<h>ENDOGENEITY/EXOGENEITY IN THE CONTROL SENSE</h>
-------------------------------------------

As I have already shown, the endogeneity/exogeneity of money can be understood in a few
distinct ways. However, most authors focus on the control sense. In that sense, the
exogeneity of the money supply implies that “its nominal size is or can be controlled by
the monetary authorities and does not automatically change as people make payments or try
to build up or run down their money holdings” (Yeager, 1997, 131). Endogeneity in the
control sense means the opposite. Graphically, the debate may be expressed using the IS/LM
framework. A vertical LM curve expresses the notion of full exogeneity, as the supply of
money is fixed and unresponsive to money demand. The second extreme case is the horizontal
LM curve, which implies a perfectly elastic supply of money and money endogeneity. The
central bank sets the interest rates at which it supplies money on demand. To resolve this
debate, one must first clarify the concepts of “money supply” and “control.” Obviously,
the central bank does not directly control the total supply of money. Nobody argues
otherwise. However, monetarists claim that the monetary authorities control the monetary
base and that there is a strong link between it and the broader monetary aggregates; hence
the money supply as a whole can be taken as exogenous. The assumption of such a link is,
of course, necessary, because the money supply in the contemporary monetary system
consists mainly of the liabilities of the banking system. Therefore monetary policy relies
on the banking system: its actions have to be transmitted by the banking system to exert a
desired effect on the total money supply. The theory that links the behavior of central
banks and commercial banks (or the monetary base and the total money supply) is the money-
multiplier model. The money multiplier itself is an arithmetical tautology that shows how
large the total money supply can be with a given monetary base and reserve ratio. But the
monetarists make two assumptions that transform the mere tautology into theory: first, the
monetary base is exogenously determined; and, second, there is a strict link between it
and the total money supply. The nonmonetarist camp presents many counterarguments. Some
researchers focus on the first assumption, arguing that the central bank does not control
the monetary base. For example, Goodhart (1994) notes that in the modern banking system,
commercial banks convert currency into deposits (and vice versa) at par. This implies that
fluctuations in the public's demand for cash must be accommodated. Post-Keynesian
economists offer an even more radical argument, as they reverse the monetarists’ causation
between the monetary base and bank deposits. They argue that banks first grant loans based
on demand factors and perceived risk and profitability. Banks look for reserves only
later, and the central bank accommodates that demand. The fact that the central bank
supplies reserves on demand implies that the monetary base is not exogenous (in the sense
of being the source of change in the economy) but rather a function of investments and
demand for loans, or the needs of trade. So it responds endogenously to changes in the
demand for money and other developments in the economy (Chick, 1973; King, 1994; McLeay et
al., 2014b).5 Others pay more attention to the second monetarist assumption. The moderate
critics point out the instability of the money multiplier, as commercial banks can choose
to hold excess reserves while the private nonbank sector may change its preference for
cash and deposits. So the critics notice some breaks in the supposedly tight link between
control of the monetary base and control of the broad money supply. In other words, the
money multiplier is believed to be unstable—that is, the relation between base money and
total money supply changes over time in an unpredictable manner. For example, the M2 money
multiplier in the United States contracted by about 50% during the Great Depression (Von
Hagen, 2009) and also during the Great Recession, as one can see in Fig. 1. Meanwhile, as
I have already discussed, the more radical opponents of the money-multiplier model reverse
the causal link between bank deposits and the monetary base. There are two key elements of
this multiplier à rebours. First, commercial banks are no longer mere intermediaries of
monetary policy that mechanically multiply reserves given by the central bank. The post-
Keynesian model gives banks some degree of control over their own business, which is a
more plausible assumption. In consequence, there is slippage between the monetary base and
the broad money supply. Although this model weakens the case for the money-multiplier
model, it does not fully demolish it, as the slippage might be less quantitatively
important than changes in the monetary base. The second element seems more significant, as
it refers to the central bank, which is said to passively accommodate the demand for
money. Such behavior is related to being a lender of last resort. It is believed that to
adequately exercise that function, the central bank should provide liquidity on demand.6
This second component also refers to the central bank's policy-response function. The
argument goes as follows: the central bank reacts to economic developments; hence the
monetary base cannot be exogenous. Exogenous variables are those whose values are
determined outside the system under consideration. But central banks alter their policy
targets in response to developments in the economic system, implying the endogeneity of
money (Moore, 1998).7 One problem is that it is not clear what the word “control” means in
the context of the money supply. Does it mean determining the amount of money supply at
will, or just exerting a dominant influence (however that may be understood)? Another
problem is that controllability is often confused with exogeneity. Logically, the money
supply may be endogenous and either controllable, through the central bank's reaction
function, or not, because of money supply disturbances generated from within the economy
and outside the central bank's control (Palley, 2002). Similarly, the money supply may be
exogenous and either controllable, through the monetarist multiplier theory operating
under the fiat-money regime, or not, as under the gold standard. In other words, as
Fischer (1993, 248) notes, “the claim that money is a controllable policy variable does
not necessarily imply that money is exogenous in the statistical sense. The monetary
authority may not have perfect control over the monetary aggregate it targets because the
money multiplier is endogenous. Alternatively the central bank often watches several
economic variables while implementing its monetary policy, hence the quantity of money
depends on the central bank's reaction function. Moreover, it is extremely difficult to
counteract unexpected changes in aggregate demand.”

<h>ENDOGENEITY/EXOGENEITY IN THE HORIZONTALIST AND STRUCTURALIST SENSES</h>
--------------------------------------------------------------------

The debate about the endogeneity/exogeneity of money is also complicated by the fact that
there are two main strands of the endogenous-money approach. The first is horizontalism,
the most extreme version of money endogeneity. According to this view, the central bank
exogenously sets the interest rates at which it fully accommodates demand for reserves
that results from banks’ decisions to meet all creditworthy borrowers’ demand for loans.
Thus, under this approach, the money supply curve is horizontal—that is, perfectly
interest elastic, as, although the central bank sets the short-term interest rate, it has
to always accommodate bank demand for reserves in order to preserve the stability of the
financial system (Moore, 1998). The second strand is the structuralist view. It also
adheres to the core proposition of the endogenous-money approach that bank lending drives
the money supply. However, the structuralists additionally take account of the role of
portfolio preferences, uncertainty, balance sheet positions, profit-seeking behavior,
microeconomic financial constraints, financial innovations, and expectations in
influencing the money supply (Wray, 1990).8 As the structuralists accept the upward-
sloping money supply curve, they are between the verticalists and the horizontalists. The
proponents of this view argue that the central bank retains some control over the supply
of reserves and only partially accommodates the demand for them. This implies that the
central bank can decide which instrument to target and whether to accommodate demand for
reserves. That is, it does not automatically provide whatever liquidity is demanded, as it
is an active player that additionally operates under a set of constraints that affect its
ability and willingness to conduct a fully accommodative policy (Palley, 2013). Moreover,
in contrast to the horizontalist view, the structuralist approach underlines the
importance of commercial banks’ asset and liability management, which allows them to
(partly) overcome reserve constraints. Thus, according to Fontana (2003), the latter view
is broader and more sophisticated than the former. For the structuralists, endogenous
money is more than a horizontal money supply curve or the central bank's reaction
function. They also take the liquidity preference of households and banks into account,
maintaining that commercial banks are not merely quantity takers in the credit market that
only passively accommodate the demand for loans. Hence, although both groups share the
fundamental insight that bank lending drives the money supply, the horizontalists focus on
the control sense—that is, whether the central bank accommodates the commercial banks’
demand for reserves. In this approach, the endogeneity of money depends exclusively on the
monetary authority and its willingness to meet the demand for reserves. Meanwhile, the
structuralists underline in addition the banks’ asset and liability management activities.
In that approach, the endogeneity of money depends on both the central bank's behavior and
the actions of commercial banks, which are not fully dependent on the central bank
(Palley, 1994). In other words, the horizontalists claim that money is endogenous, because
central banks willingly and deliberately supply the reserves on demand. The money supply
curve is thus horizontal, as the suppliers of money always fully accommodate the demand
for money at a given interest rate. Meanwhile, the structuralists argue that money is
endogenous, because—thanks to innovative techniques of management of assets and
liabilities—commercial banks can lend largely free of any central bank constraint
(Howells, 2005). Hence, although monetary policy is effective in the short run, it is
“outwitted and subverted by the banking system in the longer term” (Chick and Dow, 2002,
588). The money supply curve is upward sloping but moves rightward in the long run.9

<h>CONCLUSIONS</h>
-----------

The conclusion is clear. The debate about endogeneity versus exogeneity of money has been
too simplified. The issue is more complex than many economists would like to admit (Chick,
1973). What complicates the matter is the fact that many participants in the debate use
the terms without proper defining them. In particular, the concepts of controllability and
exogeneity (and policy-determined and exogenous variables) are often conflated. The
problem exists because central banks have deliberately chosen to set the interest rate and
supply reserves on demand. Hence they have retained their control over the money supply at
some ultimate level but changed the way they exercise it.10. After all, central banks can
set short-term interest rates because they have a monopoly right to create money.11
Economists also confuse the worlds “control” and “influence.” This is partially
understandable as to control is sometimes defined as “to maintain influence.”12. But it is
clear that the debate is not really, or should not be, about control of the money supply,
as absolute control is impossible in our monetary system, but about initiative and
influence. Central banks might not have full control of the money supply, but as long as
they maintain a non-negligible influence on markets, it does not really matter. There is
no simple answer to the question of whether money is endogenous or exogenous. Money can be
either endogenous or exogenous, depending on several factors. For one thing, it depends on
the components of the money supply. The question is too general, as money is too vague a
concept and money supply is too large an aggregate. In the modern economy, different
monies coexist. Commercial banks create deposits while central banks create cash and bank
reserves. Hence the debate is poorly framed and assumes a false dichotomy: the money
supply must be either determined exogenously (by the central bank) or endogenously (by the
commercial banks and the public). In reality, the money stock is jointly determined by the
interaction of the central bank, commercial banks, and the public (Brunner and Meltzer,
1981; Chick and Dow, 2002).13 The answer thus depends on its components. Commercial banks
do not control the aggregate amount of reserves (they cannot create or destroy them; they
can only transfer reserves among themselves), while central banks do not control the
banks’ deposits (banks create them when they grant loans or buy assets). Further, the
answer depends on the sense of the concept of money. For example, money is endogenous in
the origin sense, as it evolved spontaneously in the marketplace, but it is exogenous in
the evolutionary sense, as fiat currencies were imposed by governments rather than
spontaneously emerging within markets. Endogeneity/exogeneity also depends on the model
(in a statistical sense, money is exogenous in the quantity theory of money but endogenous
in other theoretical frameworks) and the monetary system (for example, money is exogenous
under the gold standard, in the sense that the money supply is outside the control of
authorities, but endogenous in the fiat system, in the sense of being elastic—that is,
being subject to central banks’ responses to the needs of the economy14). It depends on
the institutional setting. For example, Niggle (1990) distinguishes five stages of the
development of modern monetary and banking institutions. He argues that money was
exogenous in stage one (an economy with a commodity money, such as gold, or a convertible
paper currency with strict gold-backing rules) and three (an economy with a central bank
that effectively imposes reserve requirements on the banks). Stage three is an
approximation of the US monetary system in the decades immediately after the establishment
of the Federal Reserve System. However, later innovations in the form of liability- and
asset-management techniques allowed commercial banks to relax the Fed's constraints on
lending and money creation. Moreover, the Fed assumed the role of lender of last resort
for the system as a whole, which makes it unable to constrain bank-reserve growth. Hence,
“under these circumstances, even bank reserves are determined endogenously, as the central
bank acts to stabilize financial markets by accommodating the banks’ need for reserves
adequate to cover their loan-created deposits” (Niggle 1990, 448).15 Finally, the answer
depends on the central bank's behavior. The central bank might implement both active and
passive policies.16 It can sometimes accommodate the private sector's demand and react
passively to changes in the economy and banks’ behavior, but it can also initiate changes
in the marketplace. Implementing large-scale asset purchases might be the best example of
central banks’ actions on their own initiative, as they go beyond the passive reactions
that merely accommodate the banks’ demand. Hence it is practically impossible to provide
any meaningful contribution to the debate without reference to a particular context. Money
has both endogenous and exogenous aspects. It is not completely endogenous, as this would
exclude hyperinflations, which occur from time to time when monetary authorities increase
the money supply excessively.17 Such instances clearly show that central banks are not
merely passive institutions that only accommodate the demand for money. However, money is
not fully exogenous either, as that would imply that central banks are powerful while
commercial banks are powerless. But we know that monetary policy, at least the traditional
one, operates through the banking system. When it broke down in the aftermath of the
global financial crisis, central banks implemented unconventional monetary policies. Fully
exogenous money would also imply that financial crises are caused by a decline in the
monetary base. But the monetary base did not drop in any meaningful way before the Great
Recession. As Fig. 2 shows, the monetary base in the US (and other advanced countries)
increased enormously in the aftermath of the global financial crisis, as central banks
tried to counteract, effectively or not, the endogenous contraction in total credit to the
private nonfinancial sector caused by the financial crisis. Another problem with the
debate about the endogeneity/exogeneity of money is that the economists involved in it,
even if they are right in some respects, often make too far-reaching conclusions. In
particular, the post-Keynesians are right when they criticize the money-multiplier model.
It is true that the impact of monetary policy is less mechanical and more subtle than the
monetarist textbooks seem to describe. However, the fact the model is erroneous does not
imply that the money supply curve is horizontal or that central banks are powerless to
affect the money supply.18 Central banks do not affect the loan supply directly through
the multiplier, but they do affect it indirectly through the demand for loans,
creditworthiness of borrowers, value of collaterals, expected bank profitability, the
risk-taking channel of the monetary transmission mechanism, and more. So they do not
directly determine the money supply by controlling the reserve-requirement ratio and the
size of the monetary base, but only indirectly by setting interest rates. Similarly, from
the fact that the amount of loans depends on the demand for credit it does not follow that
commercial banks merely react passively to borrowers’ demands for loans. Actually, they
are active agents that set credit conditions, buy securities, or make strategic decisions.
They create money, so macroeconomists should pay more attention to their behavior.
However, it does not follow that commercial banks can create money without any
restrictions or that the supply of money is purely credit-demand driven. Central banks try
to reach certain macroeconomic goals, and they set the policy-rate targets accordingly.
The resulting monetary policy actions somehow constrain the money-creation process. In
other words, it is true that central banks can accommodate the growth in bank lending, in
line with the endogeneity of bank money, according to which commercial banks grant loans
first and look for reserves only later. This is certainly possible, and there are good
reasons to believe that this is how central banks very often indeed behave. But it is not
an inevitable result; rather, it is a matter of central bank policy. So Wray (1990) might
be right in writing that deposits make reserves as long as the central bank decides to
deliver the latter. Hence, the money supply is endogenous in the control sense, but only
because the central bank allows it to adjust.19 Analogously, the fact that the central
banks affect the money supply is not incompatible with the role ascribed to commercial
banks in endogenous-money-creation theory, according to which deposits are created
whenever banks grant loans (Chick and Dow, 2002). Therefore, in a sense, the whole debate
about endogeneity/exogeneity of money misses the point. The dichotomy between central
banks’ affecting the economy through the money supply or through interest rates is false.
Monetary policy “generally consists of a combination of quantity effects and price
effects, none of which is deterministic” (Chick and Dow, 2002, 605). What really matters
is not what the central bank's target is and whether money is exogenous or endogenous in a
control sense, but whether money is created out of thin air. In our monetary system, when
the bank advances the entrepreneur a loan, it is not the transfer of existing purchasing
power, but “the creation of new purchasing power out of nothing … which is added to the
existing circulation” (Schumpeter, 1934, 106). This is of great importance because money
is created with the simultaneous creation of an asset and a liability by the banking
sector. The implication is that—contrary to mainstream economics, in which credit remains
invisible and irrelevant, as commercial banks are considered merely intermediaries—changes
in the aggregate level of debt are of great macroeconomic importance and credit expansion
endangers financial stability. In other words, what really matters is not whether central
banks target the supply of money or interest rates, but whether they affect the money
supply at all—whether the quantity of money is determined solely by market forces.
Contrary to the real-bills doctrine and post-Keynesian monetary theory, the fact that
money is endogenous does not mean that credit expansion, and the resulting malinvestments
and misallocation of resources, is endogenous to the market economy. Actually, the
opposite is true. As Hayek (1937) notes, cyclical activity is a standard feature of an
economy with an elastic currency—that is, an economy in which the supply of money either
wholly or partially responds to changes in the demand for money or the demand for credit.
This is an important argument against loose monetary policy and credit expansion. No
matter whether the increases in the money supply are endogenous—whether they merely
respond to the needs of trade—they still distort the economy.20


<h>REFERENCES</h>
----------

  [1] Philip Arestis, Peter Howells. The 1520-1640 "great inflation": An early case of controversy on the nature of money. doi:10.1080/01603477.2001.11490322
  [2] Karl Brunner, Allan H. Meltzer. Time deposits in the Brunner-Meltzer model of asset markets. doi:10.1016/0304-3932(81)90056-8
  [4] Victoria Chick, Sheila Dow. Monetary policy with endogenous money and liquidity preference: A nondualistic treatment. doi:10.1080/01603477.2002.11490345
  [9] Giuseppe Fontana. Post Keynesian Approaches to Endogenous Money: A time framework explanation. doi:10.1080/09538250308431
  [11] Charles Goodhart. The endogeneity of money. doi:10.4324/9780203467473-10
  [14] Hans Hermann Hoppe. How is fiat money possible? - or, the devolution of money and credit. doi:10.1007/BF01101942
  [28] Thomas I. Palley. COMPETING VIEWS OF THE MONEY SUPPLY PROCESS: THEORY AND EVIDENCE. doi:10.1111/j.1467-999X.1994.tb00013.x
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<ART>Experimental evidence on post-program effects and spillovers from an agriculture-nutrition program
================================================================================

Authors: Andrew Dillon, Lilia Bliznashka, Deanna Olney
DOI: 10.1016/j.ehb.2019.100820
Year: 2020
ASJC codes: 2001
Keywords: Agricultural production, Burkina Faso, Childhood nutrition, Randomized control trials, Spillover effects

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Integrated agricultural-nutrition programs are often implemented under the premise that program effects are durable and spillover. This paper estimates one year post-program effects, three-year aggregate program effects and spillover effects using treated and untreated household cohorts. Two treatment interventions implemented agricultural interventions with behavior change communication strategies varying implementers using either village health committees or older female leaders. In the post-program period, program effects deteriorated relative to program period impacts documented in Olney et al. (2015), but the three-year agricultural, nutrition knowledge, health care practices and severe anemia impacts remained statistically significant. Despite the non-rival nature of nutrition education and promoted production techniques, there is little evidence of agricultural technology or health knowledge spillovers to non-treated households within treatment communities. Spillover effects measured for appropriate treatment of diarrhea (10 pp increase in giving rehydration salts rather than traditional medicine), wasting (20 pp lower probability of wasting) and children's anemia status (7 pp reduction in severe anemia) significantly improve in later cohorts. The aggregate program effects and spillovers are generally robust to multiple hypothesis testing.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Post-program and spillover effects are often intended consequences of agriculture and
nutrition programs designed to increase their potential effect over time (World Bank,
2007). Programs may have spillover effects if they generate non-rival goods which diffuse
in communities or, to the contrary, lead to disadoption after the program implementation
period because monitoring, knowledge decay or the return on the productive or nutritional
investment is no longer positive. The technology adoption literature provides many
examples of the diffusion of new technologies (Munshi 2004, Bandiera and Rasul 2006,
Beaman et al., 2015), the diffusion of knowledge about new technologies (Beaman and
Dillon, 2018) and the disadoption after the initial period take-up (Moser and Barrett,
2006, Duflo et al., 2011, Gilligan et al., 2014). The behavior change communication (BCC)
literature in nutrition also documents increased knowledge, yet low adoption of improved
infant and young child feeding (IYCF) practices, in response to nutrition education
campaigns (World Health Organization, 2010). Estimation of post-program and spillover
effects due to nutrition interventions is limited in the developing country context
(Benjamin-Chung et al., 2017), though in developing countries health spillovers between
siblings (Ho, 2017) and from health education programs (Mora et al., 2015) have been
documented. This paper builds on these two literatures by, first, testing whether program
impacts endure in the first year after program implementation ends among treated
households, and second to test for spillover effects by estimating whether implementation
period agricultural and nutritional program impacts estimated in Olney et al. (2015) are
also measured in non-treated households in treatment villages. We disentangle the
mechanisms of nutritional post-program effects and spillovers by estimating treatment
effects on nutritional ‘inputs’ such as mothers’ health and nutrition knowledge and
agricultural production mechanisms independently. To estimate spillovers of agricultural
production techniques, health knowledge, and children’s nutritional status, we build on a
cluster-randomized control trial conducted in partnership with Helen Keller International
(HKI) in Burkina Faso. From 2010–2012, HKI implemented an Enhanced Homestead Food
Production (EHFP) program in Burkina Faso with the specific objectives of improving
women’s agricultural production of nutrient-rich foods and children’s nutritional status.1
Two treatment groups received a standardized production intervention and a nutrition
behavior change communication (BCC) intervention with the only difference between the two
treatment groups being the BCC implementers: either older women leaders (OWL) or health
committee (HC) members. The production interventions were standardized across each
treatment group focused on knowledge of the nutritional content of specific foods that
were locally grown to encourage adoption, access to inputs, including seed and tools, to
establish village gardens, and materials to encourage the establishment of a homestead
garden. It was expected that the program would have the biggest impact on improving the
nutritional status of children during the first 1,000 days of life, therefore households
with children 3–12 months of age were targeted by the program. Mothers with children 3–12
months of age living in the treatment villages were invited to participate in the EHFP
program, along with their husbands and children. Our previous analysis of the program
impacts (Olney et al., 2015) was based on the analysis of a baseline study that was
conducted between February and May 2010 and an endline study that was conducted between
February and June 2012. In 2012, during the endline study, an additional cohort of younger
children 3–12 months old were sampled in treatment and control villages. A post-treatment
follow-up survey was also administered between March and June 2013 to track this younger
cohort of children, their mothers and households, in addition to the original households
interviewed in treatment and control villages at baseline. The EHFP program was successful
in improving women’s agricultural production during the program implementation period,
specifically women’s production of vitamin A-rich foods. No additional agricultural
treatment effects on treated households or non-treated households were found after the
program implementation period. Women’s use of manure and fertilizer decreased in the post-
program period, though manure use and number of plots cultivated by women were still
statistically significantly higher over the three-year period of the study in treatment as
compared to control villages. Increases in women’s production of vitamin A-rich crops
found during the program implementation, however, were not sustained in the post-program
period. These results suggest that program extension advice, monitoring and input
provision were critical to the small production gains found during the program
implementation period. No spillover effects on new cohort households were found in terms
of utilization of inputs or production outcomes. We also found positive program effects on
mothers’ knowledge of optimal IYCF and hygiene and healthcare practices as compared to
non-treated mothers. The analysis of the post-program period impacts suggests that
mothers’ health and nutrition knowledge deteriorated after the end of the program, though
knowledge gains were statistically significantly higher among treated as compared to non-
treated mothers for the over the three-year period of the study. Spillovers on health care
practice knowledge and exclusive breastfeeding practices for children less than six months
of age were estimated between treatment village cohorts. We estimate a 23 percentage point
increase in later OWL treatment village cohorts on exclusive breastfeeding of children
less than 6 months old. In the HC and OWL later treatment cohorts, there was a 10–11
percentage point decrease in treating diarrhea with traditional medicine and in the HC
treatment cohorts, a corresponding 10 percentage point increase in giving rehydration
salts for diarrhea treatment. With respect to children’s nutritional outcomes, the primary
findings during the program implementation period were that the EHFP program improved
hemoglobin concentration and decreased the prevalence of anemia, wasting and diarrhea
among children living in HC villages relative to those living in control villages (Olney
et al., 2015). In the post-implementation period, no further increases in hemoglobin
concentration were found. However, the relative increase in hemoglobin concentration that
was found among children 3–5.9 months of age at baseline were sustained one-year after the
program ended, although the impact estimate for the three-year study period was only
marginally statistically significant. No spillover effects were measured on the new cohort
of children 3–12 months of age at endline in the post-implementation period in terms of
their anemia status or hemoglobin level. During the program (2010–2012), the prevalence of
wasting among children 3–12 months of age at baseline living in the HC villages relative
to those living in the control villages decreased significantly by 8.4 percentage points.
In the three-year estimates, the prevalence of wasting in HC villages had declined by 5.4
percentage points more as compared to control villages, but this difference was not
statistically significant. In addition, there is some evidence that there were significant
protective effects of the program on preventing wasting among children born into treated
households during the program period. In control villages, the prevalence of wasting
increased from 2012 to 2013 among children 3–12 months of age. In 2012, there was no
change in wasting in OWL villages, and in HC villages there was a decline, resulting in
19.5 and 20.4 percentage point differences between each of the treatment groups and the
control group in the prevalence of wasting from 2012 to 2013. These differences were
statistically significant and indicate a potential role of the EHFP program in protecting
children’s nutritional status during this vulnerable age. Because there are multiple
hypotheses for agricultural, knowledge, practices, or nutritional set of measures, we
correct all estimates using multiple hypothesis testing following Anderson (2008) to
assess the robustness of our results. Among the statistically significant effects
estimated for the post-program period, three year overall program effects or spillover
effects, we report corrected p-values that account for multiple hypothesis testing. The
overall program effects are robust to multiple hypothesis testing (9 out of 11
statistically significant results), while only half the post-program effects are
statistically significant after multiple hypothesis corrections (3 out of 6 results). The
spillover effects are generally robust to multiple hypothesis corrections (4 out of 6
results). In the next section of the paper, we present the experimental design, while the
third section details the post-program and spillover effects identification strategy. The
fourth section presents the results, while the last section concludes.

<hs>  Program description</hs>
  ~~~~~~~~~~~~~~~~~~~

HKI’s EHFP program implemented in the province of Gourma in Burkina Faso consisted of an
agricultural production component and a nutrition and health BCC strategy. The
agricultural production activities included input distribution (e.g. seeds, saplings,
chicks and small gardening tools) and agricultural training provided by female village
farm leaders at village model farms. Program beneficiaries started their own homestead
food production activities after the receipt of inputs and training. Production activities
primarily included the promotion of micronutrient-rich fruits and vegetables, eggs and
poultry production. The BCC strategy was designed using the essential nutrition actions
framework that focuses on seven practices: women’s nutrition, anemia prevention and
control (e.g. intake of iron-rich foods and use of bednets to prevent malaria), iodine
intake, prevention of vitamin A deficiency, breastfeeding practices, complementary feeding
practices, and nutritional care for sick and severely malnourished children (Guyon et al.,
2009). Beneficiary women received bimonthly home visits from either an older woman leader
(OWL) or a health committee (HC) member who implemented through these visits a behavior
change communication curriculum during which beneficiaries were taught about optimal
health and nutrition practices, and discussed successes and challenges related to the
adoption of these practices.

<hs>  Study design and participants</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The EHFP program was evaluated using a cluster-randomized controlled trial2 to estimate
the effects of the program on agricultural production, knowledge, practices and ultimately
nutritional outcomes of young children3 . Villages in four departments in the Gourma
province (Diapangou, Diabo, Tibga, Yamba) were selected for inclusion if they had access
to water in the dry season to enable participation in the agricultural intervention.
Fifty-five villages were stratified by department and village size and randomized into
three groups: 1) control group which received no interventions (25 control villages); 2)
OWL group that received the agricultural production intervention with the BCC strategy
implemented by older women leaders (OWL) (15 OWL villages); and 3) HC group that received
the same agricultural production intervention with the BCC strategy implemented by health
committee (HC) members (15 HC villages). The two types of behavior change implementers
were selected because the effectiveness in improving knowledge and eliciting behavior
change may vary by the type of implementer delivering the messages. In rural areas, HC
members delivered health and nutrition interventions and could facilitate direct links
with health services, while OWLs were the main providers of ante- and post-natal
counseling and delivery care and thus could be more influential in changing infant and
young child feeding and care practices. Within the selected villages (n = 55) all women
with children 3–12 months of age were invited to participate in the study.4 Trained
fieldworkers explained the study to eligible households and informed consent was obtained
from either the household head or the mother of the selected child. We used a longitudinal
design and followed the same households, mothers and children over the two-year program
implementation period. The baseline study was conducted between February and May of 2010
(when children were 3–12 months of age), and the endline survey between February and June
of 2012 (when children were 24–40 months of age). In 2012, during the endline study, an
additional cohort of younger children 3 to 12 months of age was sampled in treatment and
control villages from both treated households, who participated in the EHFP program or
impact evaluation, and from a new cohort of non-treated households in both treatment and
control villages. A post-treatment follow-up survey was administered between March and
June 2013 to track this younger cohort of non-treated children, and their households, in
addition to the original treated households, mothers and children interviewed in treatment
and control villages at baseline and endline. Thus, we have a cohort of treated
households, mothers and children 3–12 months of age at baseline interviewed at baseline in
2010, endline in 2012 and follow-up in 2013. In addition, we have a cohort of younger non-
treated children 3–12 months of age at endline born into the treated and non-treated
households in treatment and control villages. This younger cohort and their households
were surveyed in 2012 and again in 2013. Half of these younger cohort children are
siblings with the same mother, and the remaining are siblings with a different mother (co-
wife) and cousins due to the frequency of polygamous household structures. All age
eligible children were interviewed in both the original and follow-up cohorts.

<h>POST-PROGRAM, THREE YEAR EFFECTS, AND SPILLOVER EFFECT IDENTIFICATION</h>
---------------------------------------------------------------------

Three treatment effects are specified to measure different types of program effects after
the program implementation period (2010–2012): a post-program effect (2012–2013), a three-
year effect of the program (2010–2013) and spillover effects to non-beneficiary
households. The specifications are estimated with the following regressions for the 2010
cohort restricting the sample to treated households in OWL and HC villages and control
households from the 2010 cohort: The identification of spillover effects in our study
builds on the recent literature (Baird et al., 2018; Angelucci and Giacomo De, 2009;
Miguel and Kremer, 2004)) which uses the exogenous variation in program assignment and
eligibility status. As households were screened for treatment eligibility if households
had a child between 3–12 months at baseline and the new cohort selected in 2012 used the
same survey selection criterion, the group on whom spillovers would occur is well defined
in our data. A strength of the above econometric strategy is the direct testing of
production, knowledge, practice and nutrition outcomes which the program was designed to
impact. One statistical concern is that because there are multiple primary and secondary
effects of an integrated agriculture-nutrition intervention, our results could over report
false positive effects without corrections for multiple hypothesis testing. To address
this concern, we first present all treatment effect results. We follow Anderson (2008) to
correct treatment effect p-values within agricultural, knowledge, practices and
nutritional outcome groupings among related outcome measures that are statistically
significant to assess their robustness to multiple-inference corrections. The paper’s main
results and their robustness with Anderson’s q-values are presented in Table 5.

<hs>  Balancing tests and descriptive statistics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

To test whether the sample has statistical balance in observable characteristics between
the treatment and control groups, balancing tests on household- and child-level
characteristics are estimated for the 2010 and 2012 cohorts in Tables A1 and A2 in
Supplementary material, respectively. We report household characteristics by treatment
group, HC or OWL, and control, as well as the p-value of the test of mean equality between
the three groups for the non-attrited sample. Household characteristics such as household
size, value of men’s and women’s assets, and household head’s and mother’s educational
status were all balanced across the three groups at initial randomization in 2010. One
housing characteristic, having a dirt floor, was not balanced between the treatment and
the control groups, with higher prevalence of dirt flooring in HC and OWL villages,
indicating a lower level of housing quality. Children’s characteristics, including the
gender and age, were balanced at baseline, though children’s nutritional indicators were
not. Household attrition does not seem to be a significant source of observable
characteristic imbalance, though there are differences in attrition rates between the
treatment and control groups. In Table A2 in Supplementary material, we test the mean
equality of the same household and child characteristics at selection for the 2012 cohort7
. Though villages were not re-randomized in 2012 as the objective of collecting
information was to estimate spillover effects, we compare mean characteristics across the
treatment and control groups to assess whether treatment status potentially affected
household composition and welfare characteristics, apart from the nutritional, production
or knowledge indicators on which we could potentially observe a spillover. Table A2 in
Supplementary material reports that household characteristics, value of assets and
livestock owned, as well as children’s characteristics were well balanced across the
treatment and control groups. Children’s nutritional indicators were not all balanced
across groups, particularly children’s hemoglobin status. We test for balance between the
old and new cohorts and report those results in the Table A3 in Supplementary material.
Due to variation in agricultural production and disease environment between years, it is
not necessarily expected that cohort characteristics will be balanced between years. The
balancing tests demonstrate that household and child nutritional indicators are not
balanced between the cohorts while characteristics such as child age, child gender,
household size and women’s assets are balanced between cohorts. Differences between
cohorts motivate the inclusion of time fixed effects in the between cohort spillover
specification described above.

<hs>  Post-program, three-year program, and spillover effects</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

HKI’s EHFP program in Burkina Faso was designed to improve household agricultural
production of nutrient-rich foods and the nutritional status of the targeted children who
were 3–12 months of age at the time of the baseline study through an integrated set of
production and nutrition interventions. We estimate treatment effects of the program on
the primary outcomes – household agricultural production of nutrient-rich foods, women’s
health and nutrition-related knowledge, IYCF practices, and children’s nutritional status
including anemia and anthropometric measures. As expected, HKI’s EHFP program was
successful in increasing women’s agricultural production during the program implementation
period, particularly women’s production of vitamin A-rich foods (Table A4 in Supplementary
material). Although there was no overall impact on household or on men’s production,
impacts on women’s agricultural production were fairly consistent, albeit small, across
the different types of crops. These results are consistent with other studies that have
shown small impacts of small-scale agriculture interventions on household food production
(World Bank, 2007; Masset et al., 2012; Olney et al., 2009; Dillon et al., 2019). In the
post-program period, women’s use of manure and fertilizer decreased in the post-
implementation period, though manure use and the number of plots cultivated by women were
still statistically higher over the three-year period of the study. Increases in women’s
production of vitamin A-rich foods found during the program implementation period were not
sustained in the post-implementation period (Table 1-Panel A). While the number of plots
cultivated by women and manure use were statistically higher in the treatment groups
relative to the control over the 2010–2013 period, one-year post-program implementation
agricultural production effects were not sustained (Table 1-Panel B). These results
suggest that program extension advice, monitoring and input provision were critical to the
small production gains found during the program implementation period. No spillover
effects on non-beneficiary households were measured (Table 1-Panel C), suggesting that if
agricultural programs are expected to improve children’s nutritional status through
increased food availability, the scale of the program and post-program extension advice
are likely important program design features. In terms of health and nutrition-related
outcomes, we found a significant impact of the EHFP program on improving mothers’ health
and nutrition-related knowledge in both treatment groups compared to the control group
during the program implementation period (Table A5 in Supplementary material). Treatment
effects for the post-implementation period suggests that mothers’ knowledge deteriorated
after the program implementation, though overall knowledge gains were significant and
substantial for the three-year period (Table 2-Panel A and B). The only statistically
significant declines were with respect to knowledge of vitamin A- rich foods like dark,
green leafy vegetables in the HC group and eggs in both the HC and OWL groups. Overall
program effects including one-year post-implementation on mother’s health and nutrition-
related knowledge remained significant and ranged from 13 to 24 percentage point change in
the OWL group and 12–21 percentage point change in the HC group (Table 2-Panel B).
Following on the improvements in mothers’ knowledge, our analysis of birth cohorts at
endline indicated that mothers living in OWL villages were more likely to have exclusively
breastfed children less than 6 months old as compared to mothers living in control
villages (Table 3- Panel A). However, these estimates are suggestive as they do not track
the same cohort of birth mothers over time, so we cannot rule out that the composition of
the endline group may have also influenced some of the measured differences in IYCF
practices. A significant between cohort spillover effect was also measured among non-
treated mothers in the new cohort OWL villages. We estimate an 23 pp increase in exclusive
breastfeeding children less than 6 months of age and a 2.4 pp reduction in feeding a child
using a bottle as compared to mothers in control villages (Table 3- Panel B). In any
integrated agriculture and nutrition intervention targeted to children, the primary
outcomes of interest are children’s nutritional status indicators. The primary findings
during the program implementation period indicated improved hemoglobin concentration, and
reductions in the prevalence of anemia and, wasting among children living in HC villages
relative to those living in control villages (Table A5 in Supplementary material). In the
post-implementation period, no further increases in hemoglobin concentrations were
measured or reductions in the prevalence of anemia or severe anemia (Table 4-Panel A). In
Table 4-Panel B, most of these nutrition impacts were sustained one year after the end of
program implementation. Children 3–12 months of age at baseline living in HC villages were
5 percentage points less likely to be severely anemic as compared to those living in
control villages. Among children 3–5.9 months of age at baseline living in HC villages,
hemoglobin concentration was higher, and the prevalence of severe anemia was 9 percentage
points lower compared to children 3–5.9 months of age living in control villages. To
measure spillovers within households, the effect of the intervention on younger siblings
within treated households is estimated in Table 4-Panel C. Among the younger siblings of
the target children (children 3–12 months of age in beneficiary households in 2012), there
was a protective effect of the EHFP program on the normal increase in the prevalence of
wasting that is seen in this population over the first two years of life. Whereas the
prevalence of wasting increased from 2012 to 2013 among children that were 3–12 months of
age in 2012 in control villages, in OWL villages there was no change and in HC villages
there was a decline, resulting in a 20 percentage point difference in each of the
treatment groups and the control group. These differences were statistically significant
and indicate a potential role of the EHFP program in protecting children’s nutritional
status during this vulnerable age. We observe a rise in anemia in siblings of HC treated
children (11 pp increase) and among siblings of HC treated children 3–5.9 months (18 pp
increase), though the full sample treatment effect is not statistically different than
zero (p-value = 0.11). No other spillover effects were measured for the new cohort of
children with respect to their nutritional status estimating the spillover using a between
village specification (Table 4-Panel D). Estimating within village cohort spillover
effects, non-treated children living in HC villages were 7 percentage points less likely
to be severely anemic compared to treated children assessed at baseline (Table 4-Panel E).

<hs>  Robustness of main results to multiple hypothesis testing corrections</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As we estimate different treatment effects over varying time periods and multiple
spillover effects, Table 5 presents a summary of the main statistically significant
results by time period, noting the effect size and pvalue of the null hypothesis that the
coefficient estimate is statistically different than zero for statistically significant
treatment effects. Table 5 also presents the corrected q-values for multiple hypothesis
testing following Anderson (2008). The overall program effects are robust to multiple
hypothesis testing (15 out of 21 statistically significant results where p-values rejected
the null hypothesis that the treatment effect was equal to zero). The sustained impacts on
anemia and hand washing were not robust to multiple hypothesis testing, while the results
on women’s agricultural land holdings, inputs, breastfeeding knowledge, and nutrient rich
food knowledge were robust to multiple hypothesis testing. Three out of the seven post-
program effects are statistically significant after multiple hypothesis corrections. The
results which were not robust to multiple hypothesis testing were the results on mother’s
knowledge of vitamin A rich foods (dark leafy vegetables and eggs) and treating diarrhea
using traditional medicine. Results on agricultural inputs and breastfeeding knowledge
were robust to multiple hypothesis testing among the post-program effects. Five out of the
eight statistically significant spillover effects estimated are also robust to multiple
hypothesis correction. The results that were not robust to multiple hypothesis testing
included the within and between cohort results on breastfeeding and the anomalous result
on increased anemia prevalence among younger siblings. The spillover effects on the
treatment of diarrhea, anemia and wasting remained robust to multiple hypothesis testing.

<h>CONCLUSION</h>
----------

This paper demonstrates the importance of post-program effects in evaluating the impact of
an integrated agriculture and nutrition program where disadoption dynamics, knowledge
deterioration or spillovers may affect overall program impact assessment. Despite
deterioration of some of the program implementation period effects and limited production
and knowledge spillover effects, we found a significant impact of an agriculture and
nutrition program on improving children’s hemoglobin concentration during the program
period and sustained impacts one-year after the program ended. We also demonstrate a
potential protective effect of the program on younger children born into beneficiary
households during the program period on preventing wasting during the first two years of
life. While no impacts across treatment cohorts were estimated on children’s
anthropometric outcomes, within HC villages, younger children were statistically less
likely to be severely anemic. Production or nutrition BCC mechanisms provided some
explanation for these sustained and spillover effects. We found small effects from
increased agricultural production over the program implementation period and limited
spillovers to non-treated women from production interventions in the post-program
implementation period. Knowledge related to some optimal health and nutrition practices
deteriorated during the post-implementation period, though it remained significantly
higher than knowledge among mothers in control villages over the three-year study period.
Overall, program spillovers are limited with respect to health and nutrition-related
knowledge, except for an important decline in the belief that traditional medicine should
be used to treat children’s diarrhea. Finally, we found a statistically significant child
feeding spillover effect on exclusively breastfeeding children under 6 months of age,
though this result is not robust to multiple hypothesis testing corrections. Despite
significant positive effects during the program implementation period on hemoglobin
concentrations, several factors may explain the lack of impact on other nutritional
outcomes with respect to the between village spillovers. First, agricultural production
impacts one year after program implementation were not detected in our sample. Given these
disadoption dynamics, availability of nutrient-rich foods did not significantly change for
beneficiary households or non-beneficiary households in treatment villages. Without
program support, the agricultural component implemented over the two-year project was not
able to sufficiently resolve the production constraints including access to water during
the dry season, faced by rural Burkinabe producers. Second, agricultural production
requires labor that women with young children may not have been able to sustain after the
initial program period. Without program monitoring, the incentives to provide labor may
have decreased, resulting in lower production. With respect to the role of nutrition
education in sustaining program impacts or promoting spillovers, the impact estimates
clearly show that the modality of providing nutrition education either through health
committees or drawing on the experience of older women leaders was critical to sustaining
impacts and spillovers within beneficiary households and across cohorts. In Olney et al.
(2015), initial program period effects are likely explained by the mixed gender health
committee’s effectiveness in communicating nutrition messages, but also potentially by
having more technical health knowledge to connect mothers and children to the formal
health system. If this is the case, sustained effects and spillovers are potentially
explained through the program’s mobilization and demonstration of new roles for the health
committee and OWLs in monitoring and providing information to new mothers. These
nutritional resource people including both village health committee leaders and older
women leaders remained in treatment communities which could explain the presence of and
differences in within village spillovers. Further research on why different types of
leaders led to differences in spillovers is important to understanding the role of BCC on
nutritional outcomes. The potential integrated connectivity of households within treatment
villages either to other households or to those implementing the nutrition education
components of the program will be an area of future research which we will explore to
further understand the mechanisms driving the anemia and wasting spillover effects we
measure in this paper.


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----------

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  [9] Esther Duflo, Michael Kremer, Jonathan Robinson. Nudging farmers to use fertilizer: Theory and experimental evidence from Kenya. doi:10.1257/aer.101.6.2350
  [11] Agnés B. Guyon, J. Victoria Quinn, Michael Hainsworth, Priscilla Ravonimanantsoa, Voahirana Ravelojoana, Z. O. Rambeloson, Luann Martin. Implementing an integrated nutrition package at large scale in madagascar: The Essential nutrition Actions framework. doi:10.1177/156482650903000304
  [12] Cheuk Yin Ho. Estimating sibling spillovers in health: Evidence on symptoms. doi:10.1016/j.ehb.2017.05.003
  [13] Edoardo Masset, Lawrence Haddad, Alexander Cornelius, Jairo Isaza-Castro. Effectiveness of agricultural interventions that aim to improve nutritional status of children: Systematic review. doi:10.1136/bmj.d8222
  [14] Edward Miguel, Michael Kremer. Worms: Identifying impacts on education and health in the presence of treatment externalities. doi:10.1111/j.1468-0262.2004.00481.x
  [15] Toni Mora, Esteve Llargués, Assumpta Recasens. Does health education affect BMI? Evidence from a school-based randomised-control trial. doi:10.1016/j.ehb.2014.11.001
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  [19] Deanna K. Olney, Abdoulaye Pedehombga, Marie T. Ruel, Andrew Dillon. A 2-year integrated agriculture and nutrition and health behavior change communication program targeted to women in Burkina Faso reduces anemia, wasting, and diarrhea in children 3-12.9 months of age at baseline: A cluster-randomized controlled trial. doi:10.3945/jn.114.203539
<ART>Finance and economic growth: Financing structure and non-linear impact
======================================================================

Authors: Péter Benczúr, Stelios Karagiannis, Virmantas Kvedaras
DOI: 10.1016/j.jmacro.2018.08.001
Year: 2019
ASJC codes: 2002
Keywords: Economic growth, Finance-growth nexus, Financial development, Financial structure, Non-linearity

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Focusing on groups of high-income countries (OECD, EU, and EMU), this study shows that the finding of a non-linear, hump-shaped impact of financing on economic growth is robust to controlling for financing composition in terms of the sources (bank credit, debt securities, stock market) and the recipients of finances (households, non-financial and financial corporations), or both. In particular, we obtain the following results. First, the non-linear impact of total bank credit is more pronounced than that of either household credit alone, or the sum of bank credit, debt securities, and stock market financing. Second, credit to non-financial corporations tends to have a positive, while credit to households a negative impact on growth, even after allowing for non-linearities. Third, debt-securities and stock market-based financing have a different impact on growth. Finally, the estimated turning point of the non-linear relationship is close to that found by Cournède and Denk (2015) for the OECD countries, and lower than that established by Arcand, Berkes, and Panizza (2015) for a broad set of countries.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The relation between financial development and economic growth is much debated. As was
hypothesized by Schumpeter (1934) and supported by King and Levine (1993) with numerous
papers thereafter, differences in the level of the development of financial systems affect
economic growth differentials among countries. The impact channels vary from additional
financial funds, available to finance investment projects due to larger volumes of
savings, to more efficient reallocation of funds, thus reaching the right entrepreneurs
and leading to higher productivity (see e.g. Beck et al., 2000; Aghion et al., 2005;
Levine, 2005). The early empirical literature (see overviews ibidem or Panizza, 2014)
suggested a positive association between financial development and economic growth, the
former measured by e.g. the amount of domestic private credit or stock market
capitalization relative to gross domestic product (GDP). The dominant positive attitude
towards financial expansion encouraged a sharp increase in financial penetration, and the
median level of private bank credit (in higher income countries with data reported by the
Bank for International Settlements, BIS hereafter) constituted around 90 percent of GDP in
2014. In a number of countries, it has reached levels much greater than their GDP (see
Fig. A1 in Appendix A for some selected countries). Such high levels of financial
penetration, together with recent and contemporary financial crises started casting doubt
on the benefits of such a degree of financial deepening (see e.g. Beck, 2012). The
corresponding more recent empirical work provides evidence of either a vanishing positive
impact (as e.g. in Rousseau and Wachtel, 2011), or a potentially non-linear (often an
inverted U-shape) relationship as documented in numerous contemporary studies.1 Although
this relationship can be complex and may vary, among others, with a country's level of
economic development and quality of financial institutions (Cecchetti and Kharroubi, 2012;
Demirgüç-Kunt et al., 2013; Masten et al., 2008; Rioja and Valev, 2014), the particular
functions performed by the financial sector (Beck et al., 2014), the speed of expansion of
financial sector (Cecchetti and Kharroubi, 2012; Ductor and Grechyna, 2015), the
‘normality’ of the period under investigation (Balta and Nikolov, 2013; Breitenlechner et
al., 2015; Gambacorta et al., 2014), or the strength of patent protection (Chu et al.,
2016), the high current levels of financial penetration and the recent findings of a non-
linear impact of financial development on economic growth point to a potential of ‘too
much finance’ in many countries, thus questioning the desirability of large financial
sectors. Such findings are typically established using total finances (mostly: credit),
and the apparent non-linear impact of totals can stem from a substantial structural change
in the composition of finances, that has been taking place during the recent decades.
Though there are some studies going beyond total finances, they usually look at the impact
of certain financing components separately or using ratios, which may bias the estimation
and lead to incorrect conclusions. The main aim of this paper is to advance on this front,
and consider both the composition of finances and its potentially nonlinear impact. We
incorporate both the sources (bank financing, debt securities financing, and stock market
financing) and the recipients of finances (households, non-financial corporations, and
financial corporations). We believe that it is important to include them in this analysis
for a number of reasons. First, there is already evidence that the type of financing may
matter. Different sources of finances (bank-based versus market-based financing) can have
an uneven impact (see e.g. Beck and Levine, 2004; Cournède and Denk, 2015; Demirgüç-Kunt
et al., 2013; Gambacorta et al., 2014; Langfield and Pagano, 2016; Mishra and Narayan,
2015). At the same time, fund recipients (users of finance) might also matter nontrivially
for the outcome. For instance, Chu and Cozzi (2014) develop a model in which the nature of
liquidity constraints (whether they affect consumers or firms more) matters for the
performance and optimality of macroeconomic policies. Beck et al. (2012) stress that a
substantial household credit expansion might be hurting economic growth. In parallel,
Bezemer et al. (2014) point out that the share of credit to nonfinancial business credit
decreased sharply since 1990, while it had a significantly positive effect on growth.
Along these lines, although warning for a small sample size, Arcand et al. (2015) indeed
find that the non-linearity of household credit is more significant than that of firm
credit. Second, the analysis of the importance of financial structure is currently quite
limited. The impact of different components of financing is mostly analyzed individually
or looking only at a few of them (see e.g. Cournède and Denk, 2015), thus creating
potentially an omitted variable bias. Even when the analysis is performed including
several subcomponents together (see e.g. Gambacorta et al., 2014), the difference between
their individual and joint impact (e.g. that of total financing) is not investigated.
Besides, though the dependence of economic growth rates on bank credit financing and stock
market financing is often analyzed, the influence of debt securities is rarely considered.
Moreover, when it is, like in Langfield and Pagano (2016), the stock market and debt
securities financing is often merged, which might impose an incorrect restriction and lead
to biased inference. Finally, to our knowledge there is no study that jointly and not
individually investigates the impact of both the sources (bank financing, debt securities
financing, and stock market financing) and the recipients of finance (households, non-
financial corporations, and financial corporations), not to mention also the non-
linearity. Last, but not the least, the changing structure of financing can lie behind the
vanishing or non-linear impact of finance on economic growth;2 therefore, it is crucial to
investigate if the impact remains non-linear after controlling for the detailed structure
of finance that accounts for potential changes.3 Third, understanding of the composition-
driven versus the total-finance-driven impact on growth can shed some light on the
desirability of certain economic policies. If ‘too much of’ total finances created
problems, the curbing of the whole financial sector could be considered. If the bank
credit caused the troubles, the desirability of taxation systems promoting the debt-biased
finance should be questioned. If non-linearity and reduction of economic growth rates at
some point were connected with some structural-shift in the composition of finance, some
structural and/or competition policies could be invoked to promote the favorable
composition, and so on. Another main feature of our analysis is our focus on a homogenous
sets of (developed) countries, the OECD, EU and EMU in particular. This is important
because the empirically identified non-linearity can be an artefact of mixing different
groups of countries. For instance, Karagiannis and Kvedaras (2016) show,4 using the
original Arcand et al. (2015) data set, that their non-linearity finding vanishes when
considering more homogeneous sets of countries (such as that of the OECD, or the European
Union).5 Nevertheless, some other recent research (see e.g. Cournède and Denk, 2015;
Cournède et al., 2015; and Samargandi et al., 2015) have also concentrated on smaller sets
of more homogeneous countries like the OECD or middle-income developing countries, and
found significant non-linearity. It is of further interest therefore to investigate
whether similar results hold for the EU countries and/or the founding member states of the
European Monetary Union (EMU1999). These groups are interesting also because they are
quite homogeneous in general as well as in terms of financing structure in particular,
namely, they have strongly bank-biased financing (Langfield and Pagano, 2016). The usage
of a smaller number of more homogeneous countries and the need of detailed financial
series limit the number of observations, and influence the choice of the econometric
methodology that can be properly employed in our case. However, in order to be more
confident in the obtained empirical results, we do not restrict ourselves only to the EU
and EMU 1999 member-states samples, but also provide the results for a broader set of
countries; namely, the OECD countries where the required data are available. This does not
only enable us to compare our findings obtained using a different methodology with the
already available ones (namely, Cournède and Denk, 2015; Cournède et al., 2015), but also
allows us to be more confident in the results obtained for the EU and EMU member states,
given that the established patterns are fairly robust across all investigated groups of
countries. Our econometric research strategy is to start from a simple log-linear
specification with only few financial variables, and then to introduce richer
specifications with more detailed structure and/or non-linearity. Namely, we first
consider the impact of different types of finances (distinguished by their source and/or
recipient). This includes evaluating whether it is sufficient to use various ratios (like
bank credit to stock market, or bank credit to the sum of stock market and debt
securities, as e.g. in Demirgüç-Kunt et al., 2013, or Langfield and Pagano, 2016), or
additional disaggregation is required due to the non-homogeneity of the impact (for such
evidence see e.g. Kaserer and Rapp, 2014). Then we add a non-linear term to these
specifications. These results can be read in two main ways. On the one hand, they assess
whether the findings about the different impacts of different types of finances are robust
to the inclusion of non-linearities. On the other hand, they also explore whether a non-
linear impact remains valid after controlling for the types of finances. Finally, we
investigate the source of the non-linear effect, whether it is due to total finances, bank
credit or household credit. This last question is motivated by the findings of Beck et al.
(2012), among others, and was investigated by Arcand et al. (2015). We obtain the
following results, which prove to be quite stable in our extensive robustness analysis.
First, the non-linear impact of total bank credit is more pronounced than that of either
household credit alone, or the sum of bank credit, debt securities, and stock market
financing. Second, credit to non-financial corporations tends to have a positive, while
credit to households a negative impact on growth, even after allowing for non-linearities.
Third, debt-securities and stock market-based financing have a different impact on growth.
Finally, the estimated turning point of the non-linear relationship is close to that found
by Cournède and Denk (2015) for the OECD countries, and lower than that established by
Arcand et al. (2015) for a broad set of countries. The paper is structured as follows.
Section 2 discusses data sources and variables. Section 3 characterizes the econometric
modelling approach. Section 4 presents and discusses the main empirical findings and
Section 5 concludes. Finally, some further details and robustness checks are delegated to
the Appendix.

<h>DATA AND VARIABLES</h>
------------------

In order to evaluate the effects of the composition of domestic private finance on
economic growth and their potential role in the non-linear impact of finance on growth, we
need disaggregated data on the split of financing by the source (bank, debt securities,
and stock market financing) as well as the recipient (households, non-financial firms, and
financial corporations). For this, our most important source is the Bank for International
Settlements (BIS) database of private non-financial sector credit and debt securities, as
it provides a fairly detailed split of these series by the sources and users of finance.
Appendix A contains a detailed description of the sources of all the variables that we use
(Table A1). All the employed financial variables are expressed in relative terms to GDP
and used after the logarithmic transformation (Table 1 describes the actual
transformations of variables). This is first of all prompted by a better fit we obtained,
and also suggested by the marginal impact of credit on growth rates estimated and
presented by Cournède and Denk (2015) in their Figure 5 − using the logarithmic
transformation we obtain the same shape of the marginal impact (see Fig. 1 in Section
4.1). Whenever the original BIS data is quarterly, we use the last quarter to align the
frequency with the annual periodicity of other data. The BIS credit database contains
directly the ratio of credit to nominal GDP series (with a split by credit to households
and credit to non-financial corporations). For the outstanding debt securities (with a
split into issued by non-financial corporations and financial corporations), we calculate
these ratios to GDP using the BIS debt securities data and the GDP data from the World
Bank's (WB) World Development Indicators (WDI) database. It should be pointed out that
private bank credit data at the aggregate level (without splitting into household and firm
credit) are also available from the WB Global Financial Development Database (GFDD).
However, the GFDD credit series have a number of structural breaks, whereas the BIS credit
data are adjusted for breaks. Fig. A1 in Appendix A presents several comparisons between
data from the two sources, and those from the GFDD contain obvious structural breaks. This
motivated us to use the BIS data in the econometric analysis. To represent the stock
market financing of listed domestic companies, we use the market capitalization (in
percentage of GDP) indicator from the WDI database. It should be pointed out that the
usage of turnover ratio of domestic shares from the same database yields qualitatively
similar results, but loses the significance, which is consistent with the analogous
finding by Mishra and Narayan (2015). Another reason for preferring the market
capitalization series is that its ratio to GDP is more natural and therefore aligns better
with the other employed series that are also ratios to GDP. All the mentioned databases
were downloaded in June 2016, and the respective extract of series is available upon
request from the authors. The data period and number of observations to be used in further
estimations varies depending on the particular question/specification at hand and the
availability of data. The typical estimation period is from 1990 to 2014, whereas the
number of actually available countries varies from 9 to 23, depending on the particular
group of countries under investigation (OECD, EU, EMU1999) and data availability. The
number of countries is always displayed in the tables containing the results. In addition
to the discussed financial series, a set of usual control variables is included,
comprising GDP per capita, enrolment in secondary education, government final consumption
expenditure to GDP, trade openness to GDP, and inflation of consumer prices. These
indicators come from the WB WDI database, and are also annual. The additional
transformations of these original data are described in Table 1, and the specific choices
ensure comparability with Arcand et al. (2015).

<hs>  Modelling strategy, employed model, and parameter estimation</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Our econometric research strategy is to start from simple log-linear specifications with
only few financial variables, and then to introduce richer specifications with more
detailed structure and/or non-linearity. Namely, we first consider the impact of bank
credit, debt securities and stock market on growth, i.e., the impact of different sources
of financing. Afterwards, we further decompose finances not only by sources, but also by
fund users. Finally, we merge both specifications discussed above with non-linear
components. While presenting the whole picture, this gradual approach thus reveals also
the sensitivity of different specifications, without falling into potential problems
connected with relatively low degrees of freedom and possible overfitting if only the
richest specification were reported. The vector of explanatory variables xi,t can contain
various linear and non-linear terms (logarithms, their squares, interactions, etc.) of
economic series. The two main groups comprise the control variables and financial series
that were summarized in Table 1. Let us turn to the parameter estimation. When the number
of periods T grows to infinity, θh in Eq. (1) can be consistently estimated by e.g. the
fixed effects estimator. However, when T is fixed, due to the problem of incidental
parameters, consistent estimation of θh cannot be directly obtained from Eq. (1) and the
instrumental variable-based estimators of Anderson and Hsiao (1981, AH hereafter) or the
generalized method of moments (GMM) estimator of Arellano and Bond (1991) or Arellano and
Bover (1995) and Blundell and Bond (1998) are usually applied. In larger samples, the GMM
estimator is known to be more efficient when T is small and N is large, but it has large
biases when T is relatively large. On the other hand, the AH estimator is consistent under
both N and T asymptotics (see e.g. Phillips and Han, 2014). This last property is very
convenient in our case, because we want to estimate the impact of financial deepening on
economic growth in the sample of EMU countries, which has a very limited number of
countries, thus forcing us to rely more on the increase in T rather than N. Because of
this, and in order to increase the number of observations, we do not aggregate the initial
data into e.g. 5 or 10 years periods (as in the baseline estimations of Arcand et al.,
2015). That would not only substantially reduce the number of effective periods to a few,
but also might induce pre-aggregation bias; while the removal of business cycle effects by
such a simple aggregation is also questionable, because the length of business cycles
might vary both in time and among different countries. Consequently, the AH instrumental
variable estimator will be used hereafter. As a robustness check, we also run the Arellano
and Bond (1991) difference GMM estimator. In all the cases, the robust inference is based
on standard errors adjusted for clustering by countries.

<hs>  Caveats</hs>
  ~~~~~~~

The presented results should be considered with some caution due to several reasons.
First, given our focus on a homogenous set of developed countries (most importantly: the
EU and EMU1999), the sample size is quite limited, whereas the number of parameters is
large due to the consideration of a detailed structure of financing. To tackle this, we
use yearly data and not multi-year averages, as that would further shrink the number of
observations. In addition, to increase the number of observations we consider also a
larger group of countries (the OECD countries) and, given consistent results among various
country groups, we are more confident in the findings established for the EU and the
EMU1999. Note that a larger group can also cover potentially less homogenous countries
where the impact of financial deepening and/or its structure therefore might also differ.
Second, estimations that rely on the employed period (typically 1990–2014 or part of it)
are informative about processes that took place during these years, but might be less
indicative for other periods (either past or future). It is particularly true if there
were substantial changes in the conditions, for example if there were important
alterations of the financial structure or the inter-dependence between the structural
components. In order to account for this, we try to control as much as possible for all
relevant aspects and include all components of interest, which however limits the degrees
of freedom. Consequently, there is a tradeoff between weak inferences versus potential
biases due to omitted variables. Third, in order to avoid endogeneity stemming from
simultaneous relationships, we use lagged explanatory variables in Eq. (1), i.e., it is
always the future growth rates that are under prediction. However, this does not
completely eliminate endogeneity, as expectations about future growth conditions can
affect the choice of current levels of financial penetration, which may lead to a
correlation between the financial series and the error term. It is however difficult to
find the necessary (large number of) proper instruments needed in our case, due to the
detailed analysis of the structure. Therefore, we present our results without taking into
account this aspect. Fourth, the consideration of totals together with various levels of
subcomponents (even though in a non-linear model) might lead to multicollinearity and thus
weaken the statistical inference. Therefore, it is possible that some estimates would turn
significant when adding more data, once they become available in the future. Fifth, the
complete disaggregation of finances is not available: for example, credit to households or
financial corporations are reported from all sectors and not from banks only, data
coverage on private domestic or total outstanding debt securities varies across countries.

<hs>  Financing composition and non-linearity in bank credit</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Table 2 presents estimation results for the impact of composition with and without the
non-linear term for bank credit. In general, there are always consecutive triplets of
columns, using the same specification but for the different country groups (OECD, EU and
EMU1999). In particular, columns (1)−(3) present a basic specification with financing
split only by its source (bank credit, debt securities, and stock market). Columns (4)−(6)
refine the analysis of columns (1)−(3) by further splitting bank and security based
financing by its user. Columns (7)−(9) check how much the results in columns (1)−(3)
change if one adds the non-linear component of bank credit. Finally, columns (10)−(12)
augment the more detailed split of finances of columns (4)−(6) with the non-linear
component of bank credit. Columns (1)−(3) of Table 2 reveal that even when using the log-
linear approximation of the impact of finance on growth, the impact varies substantially
(even in terms of its sign) for different types of financing: bank credit and debt
security have a significantly negative impact on growth, whereas stock market financing
tends to have a significantly positive influence. In terms of bank and stock market
financing, we find that the latter is more beneficial for growth, at least in high-income
economies. This is consistent with the evidence found in many previous papers (see e.g. an
overview by Valickova et al., 2015). In short, it is not all types of financing that
affect growth negatively. Our estimates are also economically meaningful. An increase of
the bank credit to GDP ratio from 90% to 100% (a log difference of 0.105) implies a
0.17–0.12 percentage point reduction of average growth rates.7 The impact of debt
securities and equities is proportionally smaller. The results also reveal that the impact
of the different types of sources is not homogenous. In particular, the absolute values of
the coefficients of bank credit and stock market capitalization are significantly
different; therefore, the data does not support the use of their ratio. Next, the finding
that outstanding debt securities have a negative, while stock market capitalization has a
positive effect (see e.g. Kaserer and Rapp, 2014, for a similar finding for the EU
countries) reveals that merging/pooling all sources of market-based financing (as e.g. in
Langfield and Pagano, 2016) is not supported. Consequently, the equal promotion of
different types of market-based financing can be suboptimal from an economic policy point
of view. Turning to the impact of an even more refined financing structure (both by
sources and users of finance) presented in columns (4)−(6), we confirm earlier findings
that bank credit to households is a drag on economic growth, whereas bank credit to firms
tends to promote economic growth rates significantly. A similar though somewhat weaker
conclusion can be drawn about the importance of the structure of outstanding debt
securities. Namely, the coefficient of debt securities issued by financial corporations
tends to be significantly negative, whereas that of debt securities issued by non-
financial corporations is insignificant. Hence, economic growth would have been higher
during the analyzed period if outstanding debt securities were issued more by non-
financial corporations than by financial corporations. Nevertheless, the coefficient of
debt securities of non-financial corporations is still negative. Although it is
insignificant, this negative sign contrasts sharply with the positive coefficient of stock
market capitalization, which also tends to be significant. As columns (7)−(9) show, the
same conclusions are robust to the introduction of the non-linear impact of bank credit
(CREDIT2). The only difference is that the linear term is positive for bank credit, while
the quadratic term is negative. Thus, the non-linear impact of bank credit remains
significant (at least at the 10% level) after taking into account the split by the source
of financing. The finding that the linear term is positive while the quadratic term is
negative implies that there is a turning point in the impact of bank credit on growth (see
the end of this subsection for a detailed analysis of this). It should be pointed out that
CREDIT and CREDIT2 are highly correlated by construction, which is partly responsible for
the moderate significance of CREDIT and CREDIT2 observed in the OECD and the EU. Looking
the other way round, i.e. at the stability of results about the role of financial
structure to the inclusion of the non-linear term, a few changes emerge. First, the
findings about the relative benefits of promoting stock markets become even stronger as
the coefficients of stock market capitalization become larger and more significant. Next,
the differentiation between the influences of different types of debt securities becomes
more blurred. Similarly, the positive impact of bank credit to non-financial corporations
becomes significant only in the EMU1999 case (although there it becomes more significant
than without the non-linear term). Nevertheless, the relative inferiority of credit to
households remains strongly valid. Summarizing the main findings of this analysis, we find
that the impact of finance on economic growth differs substantially among the different
types, and these findings are robust to the presence or absence of the non-linear bank
credit term. During the analyzed period, bank credit was on average a drag on economic
growth rates, but the bulk of this stems from the negative impact of household credit.
Nevertheless, the non-linear impact of bank credit is robust to controlling for the main
structural composition of financing, both in terms of its source and its user. Therefore,
a part of reduced growth can also come from the non-linear impact of ‘too much credit’,
given that most countries in our sample have already reached credit levels higher than the
turning point (peak of maximum contribution of credit to growth, to be characterized
shortly). Higher stock market capitalization seems to be robustly connected with higher
economic growth, whereas larger outstanding debt securities to GDP have a negative impact
(and significantly so for financial corporations, when the non-linear credit term is
absent). Although these conclusions might be specific to the period under investigation,
they are quite robust despite substantial changes in model specifications. Finally, let us
discuss the estimated turning points of the non-linear impact of bank credit on growth
rates. Fig. 1 plots the marginal impact of bank credit on growth, with the turning point
estimate identified where the marginal impact equals zero. First, it can be seen that the
estimated turning point is smaller when finance is split only in terms of sources. In this
case, it is below 50% of GDP and varies from 37% to 46% depending on a group of countries.
Furthermore, considering the 95% confidence bounds, the marginal impact of financing here
is never found to be significantly positive. On the other hand, the positive contribution
becomes significant when a more detailed split of financing is employed (also by the user
of finance). In this case, the turning point also increases and ranges from 61% to 72% in
the different country groups. It is interesting to note that these point estimates (in
particular, 62% of GDP for the OECD) compare well with that obtained by Cournède and Denk
(2015) for the OECD countries, using a longer intermediate credit series (their estimated
turning point is about 60% of GDP). However, these point estimates are in general lower
than those established by Arcand et al. (2015), using their global sample of countries.
Nevertheless, the mentioned difference is less evident once looking at the confidence
bands: for some specifications provided in Arcand et al. (2015), the difference is
statistically significant, whereas for others it is not.

<hs>  Financing structure and other non-linearity questions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In this subsection, we explore whether the non-linearity of the effect of finance on
growth is sufficiently captured by the non-linear term of bank credit alone. Maybe the
total amount of financing from all the different sources is more relevant than bank credit
alone in generating the non-linearity, conditionally either only on the sources of
financing, or the sources and users of financing. Alternatively, maybe household credit is
solely responsible for the non-linear impact of bank credit,8 thus, after taking it into
account, the non-linearity of total bank credit vanishes. In order to answer these
questions, we investigate the statistical significance of the respective non-linear terms.
Table 3 presents the corresponding empirical findings. Columns (1)−(3) include both the
non-linear term of bank credit and that of the total financing, conditioning on the
sources of financing. Columns (4)−(6) also condition on the users of finance. Finally,
columns (7)−(9) compare the relative significance of the non-linear terms of total bank
credit and of household credit only. Comparing the significance of the linear and non-
linear terms of bank credit (CREDIT, CREDIT2) and total financing (TOTAL, TOTAL2) in
columns (1)−(6) of Table 3, one can see that the impact of bank credit is consistently
more significant than that of the total financing. Although the difference is moderate in
columns (1)−(3), where we control only for the sources of finance, there is little doubt
about the substantial difference in significance when a detailed financing structure is
taken into account (columns (4)−(6)). Therefore, we can infer that bank credit seems to
dominate in the hump-shaped finance-growth relationship. One can draw similar conclusions
from columns (7)−(9), regarding the relative significance of the non-linearity of
household credit and (total) bank credit. Bank credit retains uniformly not only the sign
of both its linear and non-linear terms, but also the significance, whereas the non-
linearity connected with household credit does not only change signs irregularly, but also
becomes insignificant in the OECD and EU samples. In the EMU1999 case, the terms of
household credit are significant, but it is more likely to occur due to the small number
of observations, potentially coupled with multicollinearity of bank credit and household
credit terms (and their squares). We therefore can infer that, even after controlling for
the structure of financing in a detailed manner, the hump-shaped, non-linear impact of
finance on growth seems to be most strongly connected with (total) bank credit.

<hs>  Robustness checks and extensions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In this subsection, we summarize the implications of some robustness checks and further
extensions. We look at the impact of varying the length of future horizons (h), excluding
outlier observations, including dummy-interaction variables for the latest after-crisis
period, reducing the number of variables (dropping period effects, dropping controls,
leaving only the most significant principal component of controls), using ratios to
represent the composition of financing instead of an unconstrained estimation, additional
modeling of dynamics (by including the changes of explanatory variables or including
autoregressive terms of the dependent variable), and using a different estimator (the
Arellano and Bond, 1991, difference GMM estimator). Finally, we explore the inclusion of
some additional indicators: an index of patenting rights, and a dummy for accelerating
real housing prices. Appendix B describes the implementation details. In order to save
space, we mostly concentrate on the sensitivity analysis and extensions of the main
results provided in Table 2: either the whole table whenever possible, or a part of it,
namely, the specification which has the most detailed split of financing composition
(columns 10–12). Due to the same reason, all tables associated with the empirical
estimation results are delegated to Appendix B. The results of the performed robustness
analysis can be summarized as follows. In general, the previously discussed main findings
are quite robust to the considered deviations from the baseline specifications considered
in Table 2. The least robust one is about the impact of the composition of outstanding
debt securities: although the negative sign of debt securities issued by both the
financial and non-financial corporations is dominant, the ranking of its subcomponents
becomes less obvious in many of the performed investigations. Some additional interesting
aspects are worth singling out. First, the negative impact of household financing seems to
emerge more over longer periods, and is much smaller in shorter horizons, as revealed both
by Tables B1 and B8. Second, it should be pointed out that these robustness checks reveal
that our findings are not driven by the recent financial crisis period: they remain
present while taking into account the potential crisis period effects as in Table B3. The
results are also not driven by a few outlying countries or observations: in addition to
that they are quite homogenous among the OECD, EU, and EMU groups of countries, the
results are robust to cutting outliers and removing up to nearly a third of observations
(see Table B2). Our two extensions also yield important insights. First, in line with Chu
et al. (2016), Table B11 shows that patenting is connected with the channel through which
an increase in household financing (relative to firm financing) influences economic growth
rates. Second, Table B13 illustrates that the positive impact of stock market financing
seems to be mostly observed during periods of accelerating real housing prices, after
which economic growth is significantly lower, but less so in countries that relied more on
capital markets during the associated housing market spur. The analogous impact of debt
securities was not observed and even had a negative sign, which can be connected also with
the bank strategies to finance housing loans by issuing debt securities.

<h>CONCLUSIONS</h>
-----------

This paper contributed to the analysis of the impact of finances on economic growth by
incorporating the structure of financing and allowing for the non-linearity of the impact
of finances, in homogeneous groups of high-income countries. Our results reveal that
different types of finances (both by their sources and their recipients) have very
different effects on economic growth, and the significance of the non-linear impact of
bank credit is robust to controlling for a fairly detailed composition of private
finances, and also for an inverted U-shape relationship between patents and innovation
(and consequently, economic growth rates). Furthermore, results are very similar in all
the three high-income groups of countries considered (member states from the OECD, EU, and
EMU1999). Besides its robustness, we find the following additional features of this non-
linearity. The non-linear impact of total bank credit is more pronounced than that of
either only household credit or the joint sum of bank credit, debt securities, and stock
market financing. The estimated turning point/threshold of the identified non-linear
relationship is smaller than that established e.g. in Arcand et al. (2015) using a global
panel, while it is in line with that estimated for the OECD countries by Cournède and Denk
(2015). Therefore, a large bank credit penetration relative to GDP (especially with heavy
financing of households) might be more harmful to economic growth in high-income countries
than thought previously. At the same time, due to the dominance of bank-biased financing
in the EU, even a simple reduction of bank credit relative to GDP, e.g., by the means of
removing the debt-favoring pattern in the taxation systems, could result in improved
economic growth rates in a number of EU countries, especially if stock markets, having a
positive impact on economic growth, were promoted instead. It should be noted that the
positive impact of stock markets on growth is sometimes perceived as being driven by the
differences in the Anglo-Saxon and continental models of economic and financial systems,
but our findings reveal that this feature persists while considering only the EU or EMU
countries. We also find and/or confirm many important aspects of the role of financing
composition, even after controlling for the non-linearity discussed above. First, the
impact of bank credit to households and non-financial corporations qualitatively differ:
in our sample, the former had a strongly negative, whereas the latter tended to have a
positive impact on economic growth. Consequently, if a reduction of bank credit were
beneficial for a particular economy in general, the strongest promotion to growth could be
achieved by shrinking household credit. This established empirical finding seems to
support the hypothesis that, in the long run, household credit diverts funds of limited
supply from firms that could generate longer-lasting positive development. One potential
mechanism is the non-trivial interaction of patents with finance, as put forward by Chu et
al. (2016). Namely, whenever funds are diverted from firms towards households, financially
constrained firms fail to develop their R&D projects further, slowing down the speed of
innovation and eventually economic growth. We find such interactions to be empirically
significant. The diversion of funds from firms to households can become especially acute
during housing market booms, periods that facilitate the expansion of credit to households
by creating larger values of collateral acceptable to banks and larger returns in this
market. We indeed find that, during periods of significantly positive real housing
inflation, growth was further reduced besides what has already been captured by the
amounts of credit to households directly. Thus, either housing credit has a further
negative impact on long-term growth relative to total household credit (e.g., it may
create a drag on households’ willingness to work productively), or the actually realized
amounts of household credit do not reveal its whole negative influence (e.g., banks shrank
firm financing more by foreseeing the need of additional household borrowing in the
future). At the same time, the larger share of stock markets during the housing booms was
curbing the negative effect on growth, which might simply indicate that the bank potential
to reallocate the means towards housing was curbed, but at the same time it could point to
the importance of the development of a balanced financial system with sufficient
competition between different modes of finance. Next, the growth impact of stock market
and debt security financing are qualitatively different: stock market financing has a
positive, whereas debt securities tend to have a negative influence on growth. Looking
from both the methodological and policy perspectives, this would suggest that the use of
financing aggregates and the equal promotion of all types of market-based modes of
financing might be just as misleading as cutting all types of bank credit. Although
statistically less clear-cut, we have found some evidence that shifting currently
outstanding debt securities from financial corporations towards the non-financial ones
could be beneficial for growth. This can be due to several factors at play. First, a
substantial part of debt securities issued by financial institutions is connected to the
financing of housing, which we find to have a negative impact on growth. Furthermore,
international financial markets are highly integrated, and financial institutions issuing
debt securities can outsource domestic savings from high-income economies to other
countries easily, thus reducing the local funding of investments. On the other hand, given
the increased total globalization of corporate activities, it can be a potential
explanation also for the negative sign (though smaller absolute value) of the impact of
non-financial corporations. Finally, from the policy perspective, our results point to
several alternatives connected with the financial deepness and its structure that would
promote economic growth. Regarding the banking sector, growth could be enhanced by
directing more credit towards non-financial corporations and by reducing the bank credit
to GDP levels in a number of European countries (especially, from the EMU). The reduction
of household credit, which simultaneously diminishes the total amount of credit and
favorably changes its composition, can have the largest economic impact. However, the
effect of a reduction of the total amount of bank credit also depends nontrivially on the
initial conditions of a particular economy (namely, the actual distance from the peak
impact of credit, the level of penetration of all modes of finance, etc.). Therefore, for
economies that are close to the turning point of the non-linear impact, a balanced
compositional shift towards firm financing without affecting the total amount of credit
might be best suited. The further development of market-based financing seems to be mostly
beneficial through the fostering of stock markets. The above findings are in line with the
European Union's ongoing strategy to generate a greater choice of funding through a
diversified financial system, while making the financial system more resilient (through
the capital markets union).


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----------

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<ART>Fiscal multipliers in good times and bad times
==============================================

Authors: K. Peren Arin, Faik Koray, Nicola Spagnolo
DOI: 10.1016/j.jmacro.2015.01.002
Year: 2015  |  Pages: 303-311
ASJC codes: 2002
Keywords: Fiscal multipliers, Regime switching

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper estimates the magnitudes of government spending and tax multipliers within a regime-switching framework for the U.S. economy during the period 1949:1-2006:4. Our results show that the magnitudes of spending multipliers are larger during periods of low economic activity, while the magnitudes of tax multipliers are larger during periods of high economic activity. We also show that the magnitudes of fiscal multipliers got smaller for episodes of low growth, while they got larger for episodes of high growth in the post 1980 period. Analyzing the effects of government spending and taxes on consumption and investment spending indicates that the magnitude of the effects of fiscal shocks on consumption and investment is very small.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The role of fiscal policy in stabilizing business cycles came under scrutiny by
researchers and policymakers about three decades ago. As argued by Beetsma and Guilidori
(2011), expansionary fiscal policies implemented in response to oil price shocks did not
provide the desired results and therefore raised concerns regarding the efficiency of
fiscal policy during business cycles. Moreover, fiscal consolidations in Europe during the
1980s, contrary to Keynesian wisdom, led to an increase in output in the short-run and in
the long-run and therefore led economists and policymakers to question the established
theories regarding fiscal policy. Recent studies, including Alesina et al. (2002) explain
this puzzling result with the fact that, certain fiscal shocks, namely shocks to
government wages and salaries, can have non-Keynesian effects. They show that negative
shocks to government wages and salaries result in an increase in economic activity both in
the short-run and in the long-run by decreasing labor demand and wages, and therefore
increasing business profits and investment. With the global financial crisis of 2008
turning into a global recession, there has been a revival of interest in the effects of
fiscal policy on major macroeconomic variables. Especially in the U.S., with President
Obama’s fiscal stimulus package, there is a heated discussion regarding the effectiveness
of fiscal policy as an economic stimulus tool. In Europe, similarly, fiscal consolidations
in many countries pushed economies deeper into recession, quite differently from what we
observed in the 1980s. This particular observation certainly suggests that the magnitude-
and even the sign- of fiscal multipliers might change during the business cycle. There are
different approaches in estimating tax and spending multipliers, but the two most common
approaches employ structural macroeconometric models or vector autoregressive (VAR)
models. Among these two approaches, the VAR models occupy a more prominent role in the
recent literature. The studies using VARs identify fiscal shocks either by employing the
structural VAR approach or the narrative approach. The structural VAR approach uses either
economic theory or institutional information to identify the variance/covariance matrix,
and therefore the fiscal innovations (Blanchard and Perotti, 2002; Perotti, 2002). The
multipliers estimated with this approach are close to (in most cases less than) unity.
Perotti (2002) also argues that the tax multipliers tend to be negative but small, despite
some evidence on positive tax multipliers. Finally, he argues that the U.S. is an outlier
in many dimensions, so the responses to fiscal shocks estimated on U.S. data are often not
representative of the average OECD country. Most VAR studies reach the conclusion that the
post-1980 fiscal multipliers are smaller (Perotti, 2002; Favero and Giavazzi, 2009). This
particular result is generally interpreted as fiscal policy becoming more ineffective over
the years – most probably due to increased labor and capital mobility. The narrative
approach, identifies exogenous fiscal shocks by a narrative based dummy (Ramey and
Shapiro, 1998) or the defense news measure (Ramey, 2011) or the exogenous tax measure
(Romer and Romer, 2010a). While Ramey and Shapiro, 1998) use large exogenous increases in
defense spending, like the Vietnam War, the Korean War and the Carter-Reagan military
build-up to identify shocks to fiscal policy and Ramey (2011) constructs a new defense
news variable which measures the present discounted value of expected change in military
spending, Romer and Romer (2010b) use information from the official U.S. budget documents
to classify exogenous tax changes. Ramey (2011) estimates the spending multipliers to be
between 0.6 and 1.2, while Romer and Romer (2010a) find that an exogenous tax increase of
1% of GDP lowers real GDP by almost 3%. Among the more recent studies that do not use
VARs, Barro and Redlick (2011) estimate defense spending multipliers with two-stage least
squares, using annual data for different samples where the estimated multipliers lie
between 0.6 and 0.7. The approaches mentioned above, with the exception of Auerbach and
Gorodnichenko (2012), employ linear models in estimating the tax and spending multipliers.
A common characteristic of these studies is that the magnitude of the multipliers does not
vary over the business cycle. Auerbach and Gorodnichenko (2012) employ a regime switching
VAR where transitions across recessions and expansions are smooth. By imposing the
restriction that the U.S. economy is in recession 20 % of the time, they estimate that the
total spending multiplier is 0.57 during expansions and 2.45 during recessions, while the
defense spending multiplier is 0.8 during expansions and 3.56 during recessions. In this
paper, we investigate empirically whether fiscal multipliers are quantitatively different
in magnitude during “good times” and “bad times”. To do so, we use a multiple regime
framework first suggested by Hamilton (1989). We contribute to the literature by
estimating a non-linear model within a Markov-switching framework and obtaining government
spending and tax multipliers during periods of low and high levels of economic activity.
Our paper differs from Auerbach and Gorodnichenko (2012) in two respects. First, the
Markov switching model that we employ has different properties from the STVAR model used
by Auerbach and Gorodnichenko (2012). The model employed in this paper provides additional
information as it estimates the transition probabilities (the probability of staying in
each of the two regimes, low economic activity and high economic activity). Second,
government spending multipliers are identified from variations in the defense news
variable constructed by Ramey (2011) and the tax multipliers are identified from the
exogenous tax variable constructed by Romer and Romer (2010a). Ramey (2011) shows that
defense spending accounts for almost all of the volatility of government spending, but
also argues that shocks to government spending or defense spending can be anticipated
ahead of actual spending. This has important implications because anticipated future
changes in government spending can affect current economic activity. She shows that the
standard VAR shocks do not reflect news about defense spending accurately and that the
Ramey–Shapiro war dates Granger-cause the VAR shocks. Ramey (2011) also acknowledges that
the simple dummy variable approach does not exploit the potential quantitative information
available regarding the news about military spending and for this purpose constructs a new
measure of defense news variable, which reports the anticipated changes in defense
spending. We use this measure to identify shocks to government spending and to calculate
the spending multipliers. One major obstacle in calculating tax multipliers is
endogeneity. As GDP increases, we observe an increase in tax revenues and vice versa. This
makes the calculation of tax multipliers very difficult. Romer and Romer (2010b) argue
that most changes in revenues are endogenous responses to non-policy developments. They
analyze federal tax actions from 1945 to 2007 and identify four categories. Of these four
categories, spending-driven and countercyclical tax changes are defined as endogenous tax
changes, while deficit-driven long-run tax changes are categorized as exogenous tax
changes. We use the exogenous tax changes in estimating the tax multipliers. The non-
linear model employed in this paper separates periods of high and low states of the world
for the endogenous variable (the change in real GDP per capita scaled by the real GDP per
capita of the previous period, which can also be interpreted as per capita growth), and
therefore allows us to estimate separate fiscal multipliers for periods of low growth, and
periods of high growth. We find that the spending multiplier is 2.91 for periods of low
growth and 0.13 for periods of high growth, while the tax multiplier is −0.19 for periods
of low growth and −0.66 for periods of high growth. Our results show that the magnitudes
of the spending multipliers are larger during episodes of low growth, while the magnitudes
of tax multipliers are larger during episodes of high growth – a result that emphasizes
the importance of non-linearities for fiscal multipliers. Moreover, the non-linear
framework used in this study provides larger multipliers for periods of high growth and
smaller multipliers for periods of low growth during the post-1980 era when compared to
the whole sample period, which indicates that previous findings about the post-1980
multipliers might be biased since they do not differentiate between different states of
the economy. As a further analysis, we investigate how changes in government spending and
taxes affect investment and consumption spending. Our results indicate that consumption
spending rises during episodes of low economic activity and falls during times of high
economic activity, but only the rise in consumption during times of low economic activity
is statistically significant at the 5% level. Investment spending falls in response to an
increase in government spending during episodes of both low and high economic activity.
However, only the decline in investment during periods of low economic activity is
marginally significant. We find that both consumption and investment spending fall in
response to an increase in exogenous taxes during both episodes of low and high economic
activity, but none of the parameter estimates is statistically significant. The remainder
of the paper is organized as follows: Section 2 discusses the methodology employed in the
paper. Section 3 presents the empirical analysis and results. Section 4 concludes.

<hs>  Data</hs>
  ~~~~

We added squared government bond spread as an indicator of monetary credit conditions,
following Barro and Redlick (2011). Since the spread is endogenous with respect to GDP
growth, its lagged value is used rather than its current value. As indicated by Barro and
Redlick (2011), if the yield spread is thought as analogous to a distorting tax rate, then
the square of the spread approximates the deadweight loss from the distortion. Nominal GDP
and the GDP deflator are from the Bureau of Economic Analysis and interest rates are from
the Board of Governors of the Federal Reserve System. Nominal present discounted value of
expected change in defense spending and total population, including armed forces overseas
are from Ramey (2011) and the change in nominal exogenous tax liabilities are from Romer
and Romer (2010b). Summary statistics for the variables considered are reported in Table
1. Our dataset covers 1949:1–2006:4 (quarterly) for a total of 232 observations.

<hs>  Results</hs>
  ~~~~~~~

The null hypothesis of linearity against the alternative of Markov regime switching cannot
be tested directly using the standard likelihood ratio (LR) test. We properly test for
multiple equilibria (more than one regime) against linearity using the Hansen’s
standardized likelihood ratio test (1992, 1996). The value of the standardized likelihood
ratio statistics and related P-values (Table 1) under the null hypothesis (see Hansen,
1992, 1996) for details) provides strong evidence in favor of a two – state Markov
mean–variance regime-switching specification.2 Maximum likelihood (ML) estimates of the
model described above are reported in Table 2. The model appears to be well identified,
parameters are significant, and the standardized residuals exhibit no signs of linear or
nonlinear dependence (Ljung–Box statistics for dependency in the first moment and for
heteroskedasticity). The periods of high and low economic growth seem to be accurately
identified by the filter probabilities, which clearly separates the two regimes. Our
findings are in sharp contrast with the empirical findings of the previous VAR studies
that use linear VAR models. These studies do not make a distinction between periods of low
and high economic activity and estimate government spending multipliers mostly around 1.
An exception to these VAR studies is Auerbach and Gorodnichenko (2012), who employ a
regime switching VAR and find a government spending multiplier of 0.57 during expansions
and 2.45 during recessions. Even though there are some methodological differences between
our single-equation model employing a Markov switching framework and the regime switching
VAR model of Auerbach and Gorodnichenko (2012) and the way we identify fiscal shocks, both
approaches have similar findings that are in sharp contrast with the previous literature.
It should be noted that the spending multipliers that we have estimated are actually the
multipliers associated with anticipated changes in military spending based on news. As
argued by Barro and Redlick (2011), multipliers associated with non-defense purchases
would be more relevant to evaluate fiscal stimulus packages, but they acknowledge that
these multipliers are hard to estimate since there is a great deal of the endogeneity
between the movements in non-defense spending and real GDP and therefore they estimate
multipliers for defense spending. They argue that the defense spending multiplier would
provide an upper bound for the non-defense multiplier. Our multipliers should be
interpreted similarly. They represent an upper bound for the non-defense multiplier during
periods of high and low growth.

<hs>  Extensions</hs>
  ~~~~~~~~~~

Another issue that we investigate in this paper is related to how consumption and
investment spending are affected by changes in defense news measure of Ramey (2011) and
the exogenous tax measure of Romer and Romer (2010b) during periods of low and high
growth. The investigation of this issue is important in evaluating the predictions of the
real business cycle (RBC) theory and the Keynesian analysis. According to the RBC theory,
increase in government spending financed by future lump-sum taxes, creates a negative
wealth effect, which decreases consumption and increases employment. Increase in
employment raises the return to capital and increases investment. According to the
Keynesian analysis, an increase in government spending financed by future lump-sum taxes
increases disposable income, which leads to an increase in consumption. On the other hand,
increase in government spending also raises the real interest rate, which leads to a fall
in consumption and investment spending. The empirical evidence on this issue is mixed.
Fatas and Mihov (2001), Blanchard and Perotti (2002), Perotti (2002), Caldara and Kamps
(2008), and Mountford and Uhlig (2009) find that consumption increases in response to
government spending, while Ramey and Shapiro (1998), Edelberg et al. (1999), Burnside et
al. (2004), Cavallo (2005) and Ramey (2011) find that government spending lowers
consumption. The common thread among these studies is that they do not take into account
the possibility that the response of consumption to government spending may differ during
expansions and recessions. An exception to this is Tagkalakis (2008) who investigates the
effects of fiscal policy changes on private consumption in recessions and expansions in
the presence of binding liquidity constraints on households. Using an unbalanced yearly
panel data set (1970–2002) of nineteen OECD countries, Tagkalakis (2008) finds that fiscal
policy is more effective in boosting private consumption in recessions than in expansions.
Our methodology differs from Tagkalakis (2008) in two respects. First, we identify “bad
times” and “good times” from a regime switching model that allows for shifts in the mean
whereas Tagkalakis (2008) identifies “good” and “bad” times by extracting the cyclical
component of real GDP by applying the Hodrick–Prescott (HP) filter. Second, we use the
instruments used and suggested by Ramey (2011) and Romer and Romer (2010a) as measures of
fiscal policy to avoid problems related to endogeneity. We find that both consumption and
investment spending fall in response to an increase in exogenous taxes during both
episodes of low and high economic activity, but none of the parameter estimates is
statistically significant at the 5% or 10% level. We have some similarities and
differences with Tagkalakis (2008) in relations to empirical findings on consumption. We
both find that consumption increases in response to an increase in government spending
during “bad times”, which is statistically significant. However, our results indicate that
the impact of government spending on consumption is very small in magnitude. We find that
consumption decreases during expansions in response to an increase in government spending,
though this is not statistically significant. Tagkalakis (2008) finds a statistically
significant increase in consumption during expansions, though not as big as in recessions.
We find a decrease in consumption in response to an increase in taxes, while our findings
are not statistically significant. Tagkalakis (2008) has similar, but statistically
significant results. We interpret Tagkalakis’s findings as strong evidence and ours as
weak evidence for Keynesian models. The differences could be due to different
methodologies and different data sets employed.

<h>CONCLUSION</h>
----------

By identifying fiscal policy shocks, using the narrative approach, we estimate the
magnitude of fiscal multipliers within a non-linear framework. The empirical results show
that the magnitudes of the spending multipliers are larger during times of low growth,
while the magnitudes of tax multipliers are larger during times of high growth. Our
results imply that there is a role for fiscal policy as a stabilization tool by using the
“right instrument” at the “right time”. Another contribution of our paper is, contrary to
the previous literature, to show that multipliers during periods of low growth get
smaller, and multipliers during times of high growth get larger in the post-1980 era
relative to the whole sample period. This particular result implies that the comparison of
fiscal multipliers between periods in linear VAR studies might be biased. Analyzing the
effects of government spending and taxes on consumption and investment spending indicates
that the effects are very small. Further avenues for research may include further
disaggregation of fiscal shocks to find out exactly which budget items can be used to
stabilize the economy during recessions (or expansions). As Perotti (2002) contends that
the U.S. is an outlier in terms of response to fiscal policy actions, there is also some
benefit applying our framework to other countries, given data availability.


<h>REFERENCES</h>
----------

  [1] Alberto Alesina, Silvia Ardagna, Roberto Perotti, Fabio Schiantarelli. Fiscal policy, profits, and investment. doi:10.1257/00028280260136255
  [2] Alan J. Auerbach, Yuriy Gorodnichenko. Measuring the output responses to fiscal policy. doi:10.1257/pol.4.2.1
  [3] Robert J. Barro, Charles J. Redlick. Macroeconomic effects from Government purchases and Taxes. doi:10.1093/qje/qjq002
  [4] Roel Beetsma, Massimo Giuliodori. The Effects of Government Purchases Shocks: Review and Estimates for the EU. doi:10.1111/j.1468-0297.2010.02413.x
  [5] Olivier Blanchard, Roberto Perotti. An empirical characterization of the dynamic effects of changes in government spending and taxes on output. doi:10.1162/003355302320935043
  [6] Craig Burnside, Martin Eichenbaum, Jonas D.M. Fisher. Fiscal shocks and their consequences. doi:10.1016/S0022-0531(03)00252-7
  [9] Wendy Edelberg, Martin Eichenbaum, Jonas D.M. Fisher. Understanding the Effects of a Shock to Government Purchases. doi:10.1006/redy.1998.0036
  [13] James D. Hamilton. Analysis of time series subject to changes in regime. doi:10.1016/0304-4076(90)90093-9
  [14] B. E. Hansen. The likelihood ratio test under nonstandard conditions: Testing the markov switching model of gnp. doi:10.1002/jae.3950070506
  [16] Richard Kneller, Michael F. Bleaney, Norman Gemmell. Fiscal policy and growth: Evidence from OECD countries. doi:10.1016/S0047-2727(99)00022-5
  [17] Andrew Mountford, Uhlig Harald. What are the effects of fiscal policy shocks?. doi:10.1002/jae.1079
  [19] Valerie A. Ramey. Identifying government spending shocks: It's all in the timing. doi:10.1093/qje/qjq008
  [21] Christina D. Romer, David H. Romer. The macroeconomic effects of tax changes: Estimates based on a new measure of fiscal shocks. doi:10.1257/aer.100.3.763
  [23] Athanasios Tagkalakis. The effects of fiscal policy on consumption in recessions and expansions. doi:10.1016/j.jpubeco.2007.11.007
<ART>Heterogeneity in predictive power of early childhood nutritional indicators for mid-childhood outcomes: Evidence from Vietnam
================================================================================

Authors: Le Thuc Duc, Jere R. Behrman
DOI: 10.1016/j.ehb.2017.02.002
Year: 2017  |  Pages: 86-95
ASJC codes: 2001
Keywords: Birth weight, Child anthropometry, Education, Height growth, Vietnam, Weight gain

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We utilize longitudinal data on nearly 1800 children in Vietnam to study the predictive power of alternative measures of early childhood undernutrition for outcomes at age eight years: weight-for-age (WAZ8), height-for-age (HAZ8), and education (reading, math and receptive vocabulary). We apply two-stage procedures to derive unpredicted weight gain and height growth in the first year of life. Our estimates show that a standard deviation (SD) increase in birth weight is associated with an increase of 0.14 (standard error [SE]: 0.03) in WAZ8 and 0.12 (SE: 0.02) in HAZ8. These are significantly lower than the corresponding figures for a SD increase in unpredicted weight gain: 0.51 (SE: 0.02) and 0.33 (SE: 0.02). The heterogeneity of the predictive power of early childhood nutrition indicators for mid-childhood outcomes reflects both life-cycle considerations (prenatal versus postnatal) and the choice of anthropometric measure (height versus weight). Even though all the nutritional indicators that involve postnatal nutritional status are important predictors for all the mid-childhood outcomes, there are some important differences between the indicators on weight and height. The magnitude of associations with the outcomes is one aspect of the heterogeneity. More importantly there is a component of height-for-age z-score (at age 12 months) that adds predictive power for all the mid-childhood outcomes beyond that of birth weight and weight gain in the first year of life.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Studies on the importance of early-life anthropometry for later human capital development
recently have become prominent. Behrman and Rosenzweig (2004), Black et al. (2007),
Victora et al. (2008), Rosenzweig and Zhang (2013), and Figlio et al. (2014) find birth
weight to have significant associations with long-run adult health, education and
earnings. Gupta et al. (2011) and Krishna et al. (2016) are the most relevant previous
studies for the birth weight-related contents in our study.1 Gupta et al. (2011) use data
from the Danish Longitudinal Survey of Children (DALSC), which followed children born in
1995 with surveys in 1996, 1999, 2003 and 2007. For mid-childhood outcomes, their findings
imply that the associations of low birth weight (2.5 kg or lower) with weight and height
are statistically significant, but not the associations with behavioral outcomes. The data
used in Krishna et al. (2016) are from Young Lives, which is described in the next
section. They find that prenatal conditions, reflected in birth weight, are more strongly
associated with height trajectories than postnatal factors; they do not consider weight
and educational outcomes. A number of child health and nutrition researchers have focused
on the concept of a critical window for investing in early childhood nutrition during the
first 1000 days after conception (Martorell et al., 1994; Victora et al., 2008, 2010;
Prentice et al., 2013; Lundeen et al., 2014). Stunting at age 2–3 years, which is
indicated by deficits of two standard deviations or more below the median height-for-age
for a well-nourished reference population, has become an important policy concern (Engle
et al., 2007, 2011; Grantham-McGregor et al., 2007; UNICEF, 2013; Richter et al., 2016).
Inadequate prenatal nutrition results in low birth weight and inadequate postnatal
nutrition results in low weight and height gains in early childhood. There have been few
studies that focus on the impacts of infant weight gain and height growth. Even fewer
studies investigate the relative importance for predicting later development of weight
gain versus height growth. Huang et al. (2013) reviews the limited literature on the
predictive power of infant weight gain and height growth and reports substantial variety
in the findings. Li et al. (2004) find that height growth during the postnatal period
(birth to age 2 years) is the only variable predictive of Guatemalan women’s educational
achievement and weight gain is not statistically significant. Corbett et al. (2007) find
in UK data that “postnatal weight gain in the first 2 years of life is at most weakly
related to cognitive and education attainment at age 10. In contrast, birth weight is
clearly associated with cognitive and educational attainment at age 10…” (2007: 62). There
is, however, an issue that may affect Corbett et al’s results: factors such as birth
order, maternal education and family environment are not included in their analysis. More
recently, Huang et al. (2013) evaluated the relative associations of birth weight and
postnatal growth (weight gain, height growth, or head circumference growth) with cognition
and behavioral development in over 8000 Chinese children. They find that, for full-term
children, both birth weight and postnatal growth are associated with child’s IQ at age 4–7
years, but the sizes of the associations are small. While Huang et al. (2013) used up to
seven years for their postnatal period, we consider the postnatal period of the first
year, which is within the usually-emphasized critical window. We study the nexus of the
early childhood undernutrition with anthropometric and educational outcomes in mid
childhood. There are many studies that use height-for-age z-scores to predict longer-run
outcomes and many that use birth weight (e.g., Crookston et al., 2013; Victora et al.,
2008). While height-for-age is often interpreted to measure the nutritional status over
the whole period from conception to measurement, weight-for-age is expected to have an
advantage in capturing the effect of recent health shocks before the survey, such as
diarrhea in the few months before the survey. In the same vein, weight gain after birth
might be relevant in addition to birth weight and weight-for-age. The timing of the impact
is important because of the debate on the “critical period” during which brain development
is most sensitive to poor nutrition. Dobbing (1976), for example, argues that the period
from birth to six months is the most critical. For other authors, such as Doyle et al.
(2009), the prenatal period is more important. To separate the pre- versus postnatal
influences of nutrition status, we apply two-stage procedures in which we derive
indicators of unpredicted nutritional changes. We define the unpredicted weight gain
(height growth) in the first year of life as the component of weight-for-age (height-for-
age) z-score at age 12 months that is unpredicted based on what is known at birth,
including birth weight. Further, we define the conditionally unpredicted height-for-age as
the component of the unpredicted height growth that is uncorrelated with weight-for-age at
age one year. The conditionally unpredicted height-for-age is useful for comparison of
predictive powers of the indicators on height growth versus that of weight gain in the
first year of life. The sample of children we work with in this study differs from those
in the aforementioned studies on birth weight in a number of dimensions. Our data contain
no twins, so the distribution of birth weight differs from that in the papers that use
data on twins since the distribution of birth weights for twins is to the left of the
distribution of birth weights for singletons.2 In part because our data do not have twins,
less than five percent of children in our sample have birth weight under 2.5 kg (the
standard cutoff for low birth weight), even though we use a semi-purposeful pro-poor
sample from Vietnam. Also the age patterns of undernourishment are very different than
reported for other contexts in previous studies. In the first decade of the 21st century,
for Vietnamese under-5 years old moderate and severe stunting rates were as high as those
for West and Central Africa, while the Vietnamese percentage of low birth weights was the
same as for high-income countries (UNICEF, 2009). We examine different combinations of
variables for birth weight, weight-for-age, height-for-age, unpredicted weight gain
(height growth) and conditionally unpredicted weight-for-age (height-for-age), together
with a set of controls, to estimate their associations with mid-childhood outcomes. We
find that a standard deviation higher unpredicted weight gain (height growth) in the first
year of life generally is more associated with positive outcomes in mid-childhood than are
the adverse outcomes associated with a standard deviation lower birth weight. This
suggests that for most of the children, the adverse outcomes related to being born low
weight may be partially or totally avoided by weight gain (height growth) in the first
postnatal year. In addition to the question of prenatal versus postnatal timing, we also
investigate another aspect of heterogeneity of the relationships of the early childhood
nutrition indicators and mid-childhood outcomes: the difference between height and weight.
We find that height-for-age z-score at age one year contains a component that adds
explanatory power for the variation of all the mid-childhood outcomes, beyond that of
birth weight and weight gain in the first year of life.

<hs>  Young lives data for Vietnam</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The sample is part of Young Lives, which is an international comparative study of child
poverty. Since 2002, Young Lives has been following ∼12,000 children in Ethiopia, India,
Peru and Vietnam. The Young Lives sample consists of two cohorts: ∼8000 children born in
2001–2 and ∼4000 children born in 1994–5. The Vietnamese Younger Cohort sample, which we
use in this study, consists of 20 commune-based clusters in Northern Uplands, Red River
Delta, Central Coast, and Mekong Delta. The subsamples for each of these regions contain
four rural clusters, except that for the Central Coast, which consists of four urban
clusters in the city of Da Nang and four rural ones in the province of Phu Yen. The
children in this study were on average 11.6 months old in Round 1, with the youngest being
5 months old and the oldest being 18 months old. Consistent with the design of the Young
Lives study, we limit consideration to children in the age range from 6 to 17.9 months and
therefore exclude 21 observations.3 Furthermore, following the same method as in Lundeen
et al. (2014) and Schott et al. (2013), we exclude 45 observations with anthropometric
measures in Rounds 1–3 either too low or too high or with unusually large changes (in
height or weight) from one survey round to another.4 We also drop a further 65
observations because of missing data on either weight or height in Rounds 1–3. There are
missing values on other variables discussed in the following section.

<hs>  Variables</hs>
  ~~~~~~~~~

As presented in Table 1, the characteristics of children include: sex, birth order, birth
weight, year of birth, weight at one year, and length at one year. To allow nonlinearity
in the effect of birth weight at the high end, we use a dummy variable that equals 1 for
birth weight >3.5 kg.5 The children under study are divided into two groups by birth year.
A dummy variable is defined for the children born in 2002. By the Education Law of
Vietnam, the children in this group started school one year after the ones born in 2001,
regardless of birth month. The Law was not strictly followed, however.6 Data on birth
weight were recorded in birth documents by health clinic staff at the time of birth. Other
anthropometric data were collected in the Young Lives surveys. Birth weight has missing
observations for 11% of the children. We impute values for these missing observations on
the basis of an OLS regression for the 89% of the sample that has birth weight data and
the main caregiver’s recollection (at age 1 year) of the child’s size at birth and other
relevant factors (Appendix A). We normalize birth weight in standard deviation (SD) units
for our estimates to facilitate comparisons of coefficient magnitudes across the
nutritional indicators by having them all in SD units. Supine length (Round 1) and
standing height (Rounds 2&3) were measured with length/height boards using standardized
WHO methodology (WHO, 2008) and measurements precise to 1 mm. Weights were measured
precise to a tenth of a kilogram (kg). The height (weight) measurements were converted
into height-for-age z scores (HAZ) and weight-for-age z scores (WAZ) using WHO standards
(WHO, 2006a,b; de Onis et al., 2007) based on well-nourished populations. As mentioned
earlier, child ages varied between 6 and 17.9 months in Round 1 in our sample. In the
analysis that follows, it is desirable to convert these Round 1 anthropometric measures to
the same age in months because on average in this and in most undernourished populations
HAZ declines significantly over this age range (e.g., Victora et al., 2010). Following the
method used in previous studies (e.g., Stein et al., 2010; Crookston et al., 2013; Schott
et al., 2013) we project the value of HAZ for the children either older or younger than 12
months as follows. The average HAZ for age i (in months) is defined as the mean of HAZ for
all the children age i − 1, i and i + 1 months.7 The projected value of HAZ at age 12
months is the HAZ in Round 1 for each child minus the age-group average HAZ for the actual
age of the child in Round 1 plus the average HAZ for children 12 months of age in Round 1.
That is, each child is presumed to be the same number of HAZ units above or below the
average HAZ curve for all children at age 12 months as the child was at the age actually
measured.8 The projected value of HAZ at age 12 months is denoted by HAZ1. We also apply
this method, using WAZ in Round 1 to calculate the projected WAZ at age 12 months, denoted
by WAZ1. All the outcomes are assessed at age eight years. The anthropometric outcomes are
height-for-age (HAZ8) and weight-for-age (WAZ8). The educational outcomes are the test
scores in Early Grade Reading Assessment (EGRA), math and Peabody Picture Vocabulary Test
(PPVT) the children took at age eight years. The PPVT assesses the receptive vocabulary
outcome. Cueto and Leon (2012) analyze the psychometric characteristics of the math test
and the PPVT. Household characteristics include: mother’s height, mother’s weight,
mother’s ethnicity, mother’s schooling attainment, father’s schooling attainment, and a
wealth index in Round 1. The wealth index is the simple mean of three components: (1)
housing quality, which is the scaled (0–1) mean rooms per person as a continuous variable
and dummies on floor, roof and walls9; (2) the value of consumer durables, which is the
scaled (0–1) sum of nine dummies for basic consumer durables10; and (3) the value of
health-related infrastructural services, which is the simple mean of drinking water,
electricity, sanitation facilities, and fuel, all of which are 0–1 variables.11 Regional
characteristics are represented by dummy variables for Urban, Red River Delta, Mekong
Delta, and Mountainous. We apply the official list by Committee for Ethnic Minorities of
Vietnam to define the Mountainous category.12 Mountainous areas in Vietnam are considered
less developed than other areas. Among the mountainous clusters, however, we find one with
average birth weight above that of whole sample. Looking into the details, we find high
concentration of Tay and Nung ethnic groups in this cluster. Together with the ethnic
majority of Kinh, these ethnic groups count for 84% of observations in this cluster. These
ethnic groups do relatively well in economic development, and in the decade under
research, ethnic minorities groups Tay and Nung were more prosperous than the other ethnic
minority groups in the Young Lives sample. For these reasons, we add a dummy variable for
this cluster. Similarly, another dummy variable is included for the coastal part of the
Mekong region because these sites are distinguished considerably from the other part of
the Mekong region. The gaps between the coastal and the inlands of Mekong are most
significant in parental schooling and services in general.13 Our analysis involves many
variables from multiple rounds of longitudinal data. So potentially there might be a
problem of missing values beyond that discussed above with regard to birth weight. We
find, however, that there is no concentration of missing values for any particular
variable or for any group of children. The final panel consists of 1758 observations, or
89% of the children aged 6–17.9 months from the initial sample.

<hs>  Model specifications</hs>
  ~~~~~~~~~~~~~~~~~~~~

Even though the unpredicted terms y1 and y2 correlate strongly with the corresponding
z-scores, they are not perfectly correlated so there is some leeway for having
differential predictive power. The correlation between WAZ1 and y1 is 0.90, and that for
HAZ1 and y2 is 0.86. The correlation between y1 and y2 is weaker than that between WAZ1
and HAZ1 (0.69 against 0.74). The residual y3 is orthogonal to birth weight, height-for-
age and all the regressors in X, and is therefore, orthogonal to the unpredicted height
growth y2 as well. Symmetrically, the residual y4 is orthogonal to birth weight, the
unpredicted weight gain y1 and all the controls. We consider two groups of models
corresponding to the following groupings of variables y0, z1 and z2. In both groups there
is a set of models (Models 1–2 in Group I and Models 3–4 in Group II) that include one
relation with a weight-related indicator as the dependent variables for Eqs. (1a) and (2a)
(indicated by W) and one relation with a height-related indicator as the dependent
variables for Eqs. (1b) and (2b) (indicated by H). Group I consists of models that include
zero or one of the early childhood nutritional variables: ▓▓Model C: controls only, no
variable on child nutritional status.15 ▓▓Model 0: birth weight y0 is the only nutritional
variable, e.g. β1 = β2 = 0. ▓▓Model 1W: WAZ1 represents z1, β0 = β2 = 0; ▓▓Model 1H: HAZ1
represents z2, β0 = β1 = 0; ▓▓Model 2W: y1 (Eq. (1a)) represents z1, β0 = β2 = 0; ▓▓Model
2H: y2 (Eq. (1b)) represents z2, β0 = β1 = 0. In Group II, all models contain birth weight
and one or two additional nutritional variables: ▓▓Model 3W: birth weight y0 and y1
represents z1, β2 = 0; ▓▓Model 3H: birth weight y0 and y2 represents z2, β1 = 0; ▓▓Model
4HW: birth weight y0, y2 presents z1 and y3 (Eq. (2a)) represents z2. ▓▓Model 4WH: birth
weight y0, y1 presents z1, and y4 (Eq. (2b)) represents z2. By estimation of Model C, we
will find the explanatory power of the controls, and therefore can assess how much the
nutritional variables added in the other models increase the predictive power in the
estimation of Eq. (3). Models in Group I are used for estimation of the associations for
each individual early-life nutritional variables with the outcomes. Models in Group II
contain two or three variables, of which at least one captures postnatal nutrition. These
specifications are to demonstrate the relative importance of postnatal nutritional
indicators. The purpose of Model 4HW, for instance, is to investigate if weight-for-age,
which contains y3 as a component, adds to the predictive power beyond that of the
combination of birth weight and the unpredicted height growth. On the other hand, Model
4WH permits investigation of whether the height-for-age, which contains y4, has predictive
power beyond that of birth weight and the unpredicted weight gain in the first year of
life.

<h>ESTIMATES</h>
---------

Ordinary Least Squares (OLS) regressions are used for all the estimations. We relax the
requirement that the observations be independent, allowing for the possibility that
community factors cause correlations within communes that results in heteroskedasticity.
To increase the likelihood that the standard errors are “robust” to heteroscedasticity, we
apply an option aiming at robust estimators. For the estimates in Tables 2–5 and A2 (in
Appendix B) , the Stata option used in the OLS estimations is vce(cluster community), with
community being the commune id.

<hs>  Estimates for controls</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

As described above, there is no nutritional indicators among the controls for Model C. The
estimates for Model C are presented in Table 2. It can be seen that the gender factor
(being a boy) is negatively significantly associated with height-for-age at eight years of
age. This association means that the gap in HAZ8 between eight-year boys in Vietnam and
the boys of the same age in the WHO sample is less favorable than the gap between eight-
year girls in Vietnam and the same-aged girls in the WHO sample. The estimate for gender
also implies that boys perform poorer than girls in EGRA. The gender gaps are not
statistically significant for the other outcomes. Being first-born is positively
significantly associated with anthropometric outcomes and moderately significantly
associated with EGRA. Birth year is an important predictor for the educational outcomes,
but not for anthropometric outcomes. The omitted category for the year of birth consists
of children born in 2001, so the results imply that older children perform better than
younger ones. Schooling might have been a part of reason. In fact, in the academic year
2009–10, 92% of the children born in 2001 were in grades 3–4, while only 30% of children
born in 2002 were in grade 3 or higher. Mother’s anthropometrics are significant for child
anthropometric outcomes at age eight years. With respect to the educational outcomes,
there is slight difference between the two anthropometric indicators for mothers. Mother’s
height is moderately associated with the EGRA and math tests. The children of ethnic
minority mothers perform significantly less well than those of ethnic majority mothers for
all the outcomes, except weight. Socioeconomic status (parental schooling and wealth
index) is significant for all the educational outcomes. For the child anthropometric
outcomes, the associations of mother’s schooling are statistically significant, but those
of father’s schooling are not. Finally, residing in the urban sector has statistically
significant associations with anthropometric outcomes and reading.

<hs>  Basic estimates for early childhood nutrition indicators</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As discussed in Section 2, 11% of the children have missing data on birth weight, and for
these observations, the imputed values are used in the same way as the actual data for the
regressions in Table 2. For the estimates in Tables 3 and 4, in addition to the controls
used in Model C, a dichotomous variable for “Birth weight imputed (1/0)” is included, as
well as the dummy variable on “Birth weight greater than 3.5 kg”. To ease any concern
about possible bias related to imputation of data on birth weight, we also run regressions
on the reduced sample with only observations that include birth weight data, excluding the
imputed values. The estimates are presented in Table A2 in the Appendix B. For the
remaining models, we present R2, rather than the differences, which are significant at
least for the anthropometric outcomes, unlike that for Model 0. The indicator of weight-
for-age at age one year WAZ1 in Model 1W is strongly associated with all the outcomes,
except PPVT. The goodness of fit increased from that for Model 0, and the change is most
significant for the WAZ8 outcome (0.17, or more than 50%, above that for Model C). The
estimates for the nutritional indicator in Model 1W are very similar to the corresponding
ones in Model 2W. Weight-for-age z-score at age one year and the unpredicted weight gain
in the first year of life are statistically significantly associated with reading and math
outcomes, unlike birth weight. The estimates imply that for the anthropometric outcomes,
the explanatory power of WAZ1, which includes prenatal nutrition status plus postnatal
weight gain, is slightly greater than that of y1. For the non-anthropometric outcomes,
however, R-squares in Model 1W are almost identical to the corresponding R-squares in
Model 2W, which is further evidence that variation in birth weight has little predicative
power for the educational outcomes. For Model 1H, in contrast to Models 0 and 1W, there is
a statistically significant association between the nutritional indicator, in this case
HAZ1, and PPVT. The estimates for Model 1H are very similar to those for Model 2H. The
estimate for HAZ8 in Model 1H is consistent with previous literature, such as Krishna et
al. (2016).16 The estimates for Models 3W and 3H in Table 4 are broadly consistent with
the parallel estimates in Models 2W and 2H. However, the inclusion of birth weight
together with the unpredicted weight gain (height growth) allows comparisons of the
predictive power of these variables. The estimates for Model 3W suggest that a one SD
increase in the unpredicted weight gain in the first year is associated with variation in
the anthropometric outcomes more than double of those for a one SD increase in birth
weight. For the EGRA and math scores, the estimated associations of a SD change for the
unpredicted weight gain are clearly more significant than the corresponding estimates for
a SD change of birth weight. Neither y0 nor y1 is statistically significantly associated
with PPVT. As for Model 2H, unpredicted height growth [in Model 3H] is associated
significantly with PPVT – that is not the case for the unpredicted weight gain in Models
2W and 3W. Estimates for Model 3H imply that a child born with one SD of birth weight
under the mean but with one SD of unpredicted height growth in the first year of life is
expected to have better outcomes in mid-childhood than a child born with average birth
weight who grew normally (as predicted) in the first year of life. The estimates for Model
4HW suggest that with the presence of the unpredicted height growth (y2) among the
regressors, the predictive power of the conditional unpredicted weight-for-age y3 is not
statistically significant for the height and PPVT outcomes, and for the math outcome it is
not statistically significant at five percent. Related to these estimates, the
corresponding results in Table A2 are not statistically significant for all the outcomes
in height, math and PPVT. On the other hand, the conditional unpredicted height-for-age y4
in Model 4WH is statistically significantly associated with all the outcomes. In fact, we
can see that y4 contributes to prediction of variations in anthropometric outcomes, math
and PPVT, all at the level of five percent significance. At the ten percent significance
level, one can reject the hypothesis that y4 has no association with EGRA. In Table A2,
however, the estimate for y4 is statistically significant at five percent for all the
outcomes. By definition, the conditionally unpredicted height-for-age y4 is orthogonal to
birth weight y0, the unpredicted weight gain y1 and all the control factors. That means
the variations of the outcomes that are predicted by y4 are beyond those predicted by y0,
y1 and all the control factors. Finally, it can be seen in Tables 3, 4 and A2 that there
are slight differences between the two sets of estimates concerning the magnitudes but not
the statistical significance, except for estimates for y3 and for y4 in Model 4WH and 4HW,
as discussed in the preceding paragraph. There are no such inconsistencies with respect to
the associations of the indicators with birth weight or any of the z-scores, or
unpredicted terms y1 and y2. Overall, the results in Table A2 are consistent with the
basic findings in Tables 3 and 4.

<h>DISCUSSION</h>
----------

We start with considering three standard measures of nutritional status in early
childhood. The first measure, birth weight, reflects prenatal nutritional intakes. The
second and the third are respectively the weight-for-age and height-for-age z-scores at
age 12 months, both of which incorporate both prenatal and postnatal nutritional
developments. In contrast to some previous studies we do not find strong associations of
birth weight with educational outcomes. Probably this is because in the 21 st century
Vietnamese context, low birth weight is much less prevalent than in many of the data sets
used for previous studies because of their use of twins or because they were for 20th
century low- and middle-income contexts with higher prevalence of low birth weight. The
estimates for birth weight in the current study are consistent with those in Gupta et al.
(2013). In both studies birth weight predicts anthropometric, but not the other outcomes.
Our results further are consistent with the studies related to the Dutch famine in
1944–1945. This famine led to lower birth weights of infants whose mothers experienced
severe nutritional deprivation during their pregnancy. Stein et al. (1972), however, find
that at the age of 19 years there were no detectable adverse effect on cognitive ability
of the children born around the time and location of the event. Back to the current study,
even for the outcomes for which birth weight has the most significant predictive power –
anthropometries at age eight years – it predicts a smaller part of the variance than
predicted by any of the weight or height z-scores. Weight-for-age and height-for-age
z-scores at age 12 months are strongly associated with all the anthropometric outcomes and
educational outcomes at age eight years except the former does not predict the receptive
vocabulary outcome. Together with the controls, height-for-age at age 12 months predicts
half of the variation in height-for-age at age eight years (more than that predicted by
weight-for-age at 12 months for weight-for-age at eight years of age). Correspondingly but
not equivalently, weight-for-age at 12 months together with the controls predicts less
than half of the variation in mid-childhood weight-for-age. That is evidence for some
difference between height and weight in their predictive power – more evidence is
summarized below. Closely related to the aforementioned weight and height z-scores are
their postnatal components. We define the concepts of unpredicted weight gain (height
growth) in the first year of life as the parts of weight-for-age (height-for-age) z-scores
that are uncorrelated with birth weight and all the control factors, including mother’s
anthropometrics and household socioeconomic status. These unpredicted components of the
weight and height z-scores are substantial. In fact, the standard deviations of the
variables on birth weight, the unpredicted weight gain, and the unpredicted height growth
are 0.43, 0.92 and 0.94 respectively. The sizes of anthropometric outcomes at age eight
years associated with the standard deviation of unpredicted weight gain (height growth)
are more than double those of a standard deviation in birth weight. Unlike birth weight,
the unpredicted weight gain in the first year of life is strongly associated with two of
the educational outcomes. Unpredicted height growth in the same period is strongly
associated as well with the receptive vocabulary outcome at age eight years. Our study has
limitations, including inadequate information on birth outcomes other than birth weight
and no information on anthropometrics at age 24 months, which often has been emphasized in
the nutritional literature as particularly important (e.g., Victora et al., 2008, 2010).
With regard to the latter, however Schott et al. (2013) report that “in analysis using the
Institute for Nutrition in Central America and Panama (Guatemala) nutritional
supplementation study data (Stein et al., 2008:286), in which there were multiple measures
over the first 7 years of age, we found that HAZ measures at ages 6–17.9 months predict
well HAZ at age 24 months (for ages 6, 12, and 18 months, correlations with HAZ at age 24
months were r = 0.74, 0.83, 0.91, respectively). If similar correlations across ages also
hold for populations of Young Lives countries [in our case, particularly in Vietnam], the
cross-sectional patterns in HAZ at ages 6–18 months that were observed in the Young Lives
data represent fairly well cross-sectional patterns in HAZ that likely held for these same
children at 24 months, even if the overall distribution in HAZ may have declined fairly
substantially from 12 to 24 months.” Despite these limitations, our investigation sheds
considerable light on how, in the context of Vietnam in the early 21st century, early-life
nutritional indicators, together with family characteristics, link to latter outcomes. We
find the associations of the socioeconomic status with all the mid-childhood outcomes
consistently strong. Our estimates imply a standard deviation higher unpredicted weight
gain (or unpredicted height growth) in the first year of life has larger associations with
height and weight outcomes at age eight years than a standard deviation higher birth
weight. Parents might expect significant adverse outcomes in height and weight at age
eight years for children born with lower birth weights. However, expectations about mid-
childhood outcomes can change substantially at age one year thanks to developments that
were unforeseen at birth because the unpredicted weight gain (height growth) over the
first postnatal year are by construction independent of birth weight, socioeconomic status
and maternal anthropometry. In addition to the aforementioned difference between the
prenatal and postnatal nutrition with respect to their magnitudes of associations with the
outcomes, we find difference between the postnatal indicators on height versus weight.
That is, there is a component in height-for-age (at age one year) that adds explanatory
power for all the outcomes beyond that due to the linear combination of birth weight,
weight-for-age z-score (at age one year) and all the controls.


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<ART>Household dairy production and child growth: Evidence from Bangladesh
=====================================================================

Authors: Samira Choudhury, Derek D. Headey
DOI: 10.1016/j.ehb.2018.07.001
Year: 2018  |  Pages: 150-161
ASJC codes: 2001
Keywords: Animal-sourced foods, Dairy production, Livestock, Stunting

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Research from richer countries finds that dairy consumption has strong positive associations with linear growth in children, but surprisingly little evidence exists for developing countries where diets are far less diversified. One exception is a recent economics literature using the notion of incomplete markets to estimate the impacts of cattle ownership on children's milk consumption and growth outcomes in Eastern Africa. In addition to external validity concerns, an obvious internal validity concern is that dairy producers may systematically differ from non-dairy households, particularly in terms of latent wealth or nutritional knowledge. We re-examine these concerns by applying a novel double difference model to data from rural Bangladesh, a country with relatively low levels of milk consumption and high rates of stunting. We exploit the fact that a cow's lactation cycles provide an exogenous source of variation in household milk supply, which allows us to distinguish between a control group of households that do not own cows, a treatment group that own cows that have produced milk, and a placebo group of cow-owning households that have not produced milk in the past 12 months. We find that household dairy production increases height-for-age Z scores by 0.52 standard deviations in the critical 6–23 month growth window, though in the first year of life we find that household dairy supply is associated with a 21.7 point decline in the rate of breastfeeding. The results therefore suggest that increasing access to dairy products can be extremely beneficial to children's nutrition, but may need to be accompanied by efforts to improve nutritional knowledge and appropriate breastfeeding practices.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Worldwide, child undernutrition is increasingly recognized as a significant global health
problem and a major constraint to economic development. Child undernutrition is associated
with almost 3.1 million child deaths (Black et al., 2013), impaired cognitive development
in early childhood (Walker et al., 2011; Grantham-McGregor et al., 2007), reduced school
attainment in childhood, and lower labour productivity and wages in adulthood (Shekar et
al., 2006; Victora et al., 2008; Hoddinott et al., 2008). Nutritionists, moreover, have
increasingly emphasized that it is good nutrition in early childhood – in utero and the
first 24 months after birth – that is truly critical for ensuring healthy growth
(Shrimpton et al., 2001; Victora et al., 2010). A particularly striking nutritional
feature of developing country populations is that growth faltering appears to be
particularly pronounced from roughly 6 months of age to 20 months of age, a period that
coincides with the introduction of complementary foods that are often low in high quality
protein and micronutrients, such as rice, wheat, maize or starchy roots and tubers.
Previous research has found that calorie intake alone is not always a strong predictor of
child growth in developing countries settings (Griffen, 2016), perhaps because calorie
requirements for infants are relatively modest. Instead, many researchers point to low
consumption of animal-sourced foods (ASFs) as a critical constraint (Allen, 2003; Brown,
2003; Demment et al., 2003; Headey and Hoddinott, 2016; Neumann et al., 2002; Puentes et
al., 2016; Randolph et al., 2007). Indeed, in the absence of fortified foods, young
children cannot meet their micronutrient needs without daily intake of ASFs (PAHO/WHO,
2003). Dairy constitutes a particularly important complementary ASF for young children
because of the familiarity of its taste to exclusively breastfed children, and because of
its nutritional profile. Dairy is high in all three macronutrients (energy, fat and
protein), as well as important micronutrients such as vitamin A, vitamin B12, and calcium
(Murphy and Allen, 2003). Moreover, like other ASFs, dairy contains several essential
fatty acids that are hypothesized to be critical for processes of cellular growth and bone
formation (Semba et al., 2016). Dairy has a protein digestibility corrected amino acid
score (PDCAAS) of about 120%. Many studies also suggest dairy intake affects child growth
through a stimulating effect on plasma insulin-like growth factor 1 (IGF-1). Milk also
contains minerals such as potassium, magnesium, and phosphorus, that could also be a
factor stimulating growth, as well as lactose. Consistent with this biological evidence, a
range of research has linked linear growth to childhood dairy consumption, albeit mostly
in developed country samples (Iannotti et al., 2013; de Beer, 2012; Dror and Allen, 2011;
Wiley, 2005, 2009; Sadler & Catley 2009). In developing countries there have been
remarkably few efficacy trials of dairy supplementation on growth in infants or young
children, though several dairy consumption programs have demonstrated some impact on
linear growth at older ages (Iannotti et al., 2013).1 Because of the limitations of
experimental evidence on this subject, economists have increasingly utilized observational
or quasi-experimental analyses to explore the associations between dairy production and
child nutrition outcomes in less developed settings. In economic history studies, Baten
(2009, 2014) tests a “protein proximity” hypothesis with 19th Century European military
recruitment data from Central Europe. Utilizing the idea that fresh milk in these
economies could not be traded over large distances, he finds that adult men in closer
proximity to dairy production were substantially less likely to be too short for military
recruitment. Still other studies hypothesize that trends in milk consumption explain
longer term secular improvements in heights at later stages of economic development, such
as 20th Century Japan (Takahashi, 1984) and India (Mamidi et al., 2011). A recent paper
also examined adult heights in 42 European countries with varying levels of development.
Even after controlling for genetic factors, they found that the national supply of protein
from dairy products was the single strongest predictor of adult stature (Grasgruber et
al., 2014). A related study of 105 countries from different continents also found strong
associations between average milk consumption levels and adult male heights (Grasgruber et
al., 2016). In contemporary developing countries several studies have examined
associations between household livestock ownership and child growth outcomes, though not
all studies focus on milk-producing animals specifically. Like Baten (2009, 2014) these
studies assume (often implicitly) that fresh milk is generally non-tradable and not a
perfect substitute for powdered milk. Hoddinott et al. (2015) use two large surveys from
Ethiopia to specifically explore the association between cattle ownership, dairy
consumption and HAZ scores. They cite the fact that 90% of milk produced in rural Ethiopia
is consumed by the household producing it, implying that cattle ownership ought to be a
very strong predictor of regular dairy intake. Consistent with that conjecture they find
strong positive associations between cattle ownership and HAZ (as high as 0.47 standard
deviations in the 12–23 month age-range). They also implement placebo tests to explore the
concern that cattle ownership proxies for generic wealth effects on child nutrition.
Rawlins et al. (2014) evaluate Heifer International’s dairy cow and goat ownership
programs in Rwanda, albeit in a non-randomized quasi-experimental design with a small
sample of 217 children aged 0–59 months (precluding the possibility of detailed age
disaggregation). They find that children from households who received a goat 12 months
prior to the time of the survey saw no growth differential over controls, whereas
transfers of pregnant cows (high-productivity foreign breeds) improved height-for-age Z
scores by 0.57 standard deviations, a large but imprecisely estimated effect. Similarly,
Kabunga et al. (2017) use matching methods to gauge the impacts of adoption of improved
dairy cow varieties on HAZ of children aged 6–59 months. They find HAZ impacts of
0.48-0.49 standard deviations, though also some evidence of larger impacts for household
with greater herd sizes or larger acreage.2 Overall, there is fairly consistent evidence
that dairy cow ownership is associated with child growth in poorer populations, although
there are several limitations and caveats surrounding this evidence. First, the evidence
is confined to East African localities where cattle ownership is relatively common, so
external validity is a concern. Second, this literature potentially suffers from several
internal validity issues, including the confounding role of livestock as a source of
imperfectly measured rural wealth, and potential concerns over associations between
livestock ownership and ethnicity.3 Another outstanding concern not addressed in the
previous literature is that the availability of cow’s milk leads to premature cessation of
breastfeeding by mothers. Exclusive breastfeeding is strongly recommended for the first 6
months of life, especially in developing country settings, because of its critical role in
preventing diarrhea and respiratory infections (Horta and Victora, 2013), and because
cow’s milk can stress a newborn’s immature kidneys and irritate the lining of the stomach
and small intestine, leading to blood loss and iron-deficiency anemia (FAO, 2013). In
light of these limitations, this paper utilizes a unique dataset to attempt a more
comprehensive assessment of the nutritional implications of dairy production and
consumption in Bangladesh. Bangladesh is a particularly important case study in the
context of dairy production. In addition to its high rates of stunting (36%), Headey and
Hoddinott (2016) emphasize that Bangladesh has an under-diversified food supply, with FAO
data suggesting that ASFs account for less than 5% of total calories supplied (Headey and
Hoddinott, 2016). This situation partly stems from exceptionally low levels of milk
consumption, which in per capita terms is less than half that of neighbouring India
(Headey and Hoddinott, 2016). A likely explanation of this is the country’s exceptionally
severe land constraints (and hence feed constraints), with average farm sizes in
Bangladesh averaging just half a hectare, and rural landlessness widespread. It may also
be that cultural norms – historical unavailability of milk – has kept demand for milk
relatively low. In this paper we use the nationally representative Bangladesh Integrated
Household Survey (BIHS) of rural areas, which was conducted over two rounds in 2011/2012
and 2015. Uniquely for such a large survey, this dataset contains rich information both on
nutrition outcomes, individual food consumption, agricultural assets and production, and a
range of other potential determinants of nutrition. Methodologically, we propose a novel
difference-in-difference approach to assessing the impact of dairy cow ownership on child
nutrition outcomes, by distinguishing between households with lactating dairy cows that
have produced milk over the past 12 months (treatment), households with cows that have not
produced milk in the past 12 months (placebo), and households that do not own any dairy
cows (control). We note that this is not a placebo in the medical definition (according to
which a person consumes a treatment of no intended therapeutic value), but in the sense
that non-lactating cows might have a similar long run economic value any direct milk
supply to the household. This distinction between the treatment and placebo emerges from
the fact that smallholder dairy producers in Bangladesh typically only own a few cows
because of the extreme land and feed constraints mentioned above. Specifically, 80% of
Bangladeshi farmers in our nationally representative sample own just 1–2 cows and no
farmers in our sample own more than 4 animals. Given that at any given time all or some of
these cows will not be lactating – since there is a minimum 12-month inter-calving cycle
for each animal even among the most technologically sophisticated dairy producers – there
is a non-trivial proportion of dairy cow owners in Bangladesh who would be unable to
produce milk on a continuous basis for exogenous biological reasons.4 In effect, then, the
combination of small herds and a biologically determined component of the lactation cycle
potentially creates a valid placebo group of children who are treated with cows that have
not produced any milk. We therefore test three hypotheses: Children in treatment group
will be taller than children in control; Children in the placebo group will not be taller
than the control; and Children in treatment group will be taller than placebo group
children. In addition to these tests we also examine whether livestock ownership or milk
production is associated with other observable potentially confounding factors, such as
maternal nutritional knowledge and empowerment, and overall child diversity, exclusive of
milk. And unlike previous studies in this literature we explore the policy-relevant
question of whether access to a stable household level supply of dairy products leads to
substitution between breastfeeding and dairy milk intake. We find that milk production is
strongly associated with linear growth, but only for children in the crucial first 1000
days of life (particularly the 12–23 month range). The effects we observe are very close
in magnitude to those observed in the aforementioned quasi-experimental study by Rawlins
et al. (2014) for Rwanda and Kabunga et al. (2017) for Uganda, but larger than the more
observational study by Hoddinott et al. (2015) who analyse the impacts of owning any cow,
rather than milk-producing cows specifically (rendering their results more like an intent-
to-treat analysis). Null results for the placebo group also lend credence to the
identification assumptions underlying our approach, as do additional placebo tests which
rule out systematic differences in nutritional knowledge and women’s empowerment. However,
we do find some evidence of potentially harmful effects of household dairy availability on
breastfeeding in the first year of life, suggesting dairy-oriented nutrition strategies
need to proactively promote exclusive breastfeeding in the first six months to prevent
premature substitution into dairy. The remainder of this paper is organized as follows.
Section 2 describes the data and the methods used to analyse them. Section 3 tests
associations between different ASF production and various nutrition outcomes. Section 4
provides some important sensitivity tests and extensions, and Section 5 concludes with a
discussion of the implications of these findings for programs and policies, as well as for
future research.

<h>CONCEPTUAL MODEL, DATA AND METHODS</h>
----------------------------------

As outlined above, our objective in this paper is to test for significant differences in
milk consumption and child growth between household groups that are defined by dairy
production and cow ownership. Previous papers in this literature have tended to focus on a
comparison between a “treatment group” of households that own any dairy cow and a “control
group” of households that do not own any dairy cows. In our data we instead narrow the
definition of treatment households to those that owned cows that actually produced milk in
the past 12 months (hereafter treatment). We then define what can be thought of as a
“placebo group” of children exposed to cows that had not produced any milk in the past 12
months (note that we think of this group as a placebo because the treatment is not milk
per se - in which case the placebo would be a milk substitute - but milk-producing cows).
In an ideal experimental design children would be randomly assigned across groups, but in
observational settings a significant concern is that there may be systematic nutrition-
relevant differences between treated and non-treated children (e.g. wealth, nutritional
knowledge, women’s empowerment). Achieving more experimental conditions might therefore
require extensive control for potential confounding factors. The conceptual model
described in Hoddinott et al. (2015) is a useful starting point for thinking about the
various factors that might influence household decisionmaking processes with respect to
dairy production, dairy consumption and child nutrition. They posit a household utility
model in which child nutrition is one argument. Nutritional status is itself a function of
nutrient (food) intake, as well as nutritional knowledge, culture, healthcare, genetic
endowments, and locational characteristics (such as the prevalence of disease; access to
information about good child care practices). In a world of perfectly functioning markets,
nutrient intake would be primarily influenced by income, and households could sequentially
maximize farm and nonfarm income before deciding how to spend that income so as to
maximize nutrition outcomes subject to other arguments in the utility function. However,
the perishability of milk in poorly developed value chains renders household production
and consumption decisions non-separable. In other words, if households struggle to access
affordable milk via markets, they could opt to own dairy cows. This implies that the
decisions to own dairy cows and/or produce milk may be endogenous, influenced as it is by
nutrition knowledge and farm production parameters such as the availability of capital
(income, savings, wealth), access to land (feed), access to input and output markets to
obtain feed and sell produce, household labour supply, farm management skills, and the
role of women in household decisionmaking, including dairy production and feeding
practices. Since omission of these kinds of factors could lead to biased coefficients on
the impacts of cattle ownership or milk production on child growth, our empirical models
need to control for these factors as extensively as possible. Fortunately, the Bangladesh
Integrated Household Survey (BIHS) not only contains detailed data on children’s food
intake and nutrition outcomes, but also an exceptionally rich array of data on income,
wealth, agricultural production and assets, access to markets, women’s empowerment and
women’s nutrition knowledge (IFPRI, 2016). BIHS is also a large survey representative of
rural Bangladesh that has been implemented in two rounds (2011/2012 and 2015) and
constitutes a panel for the majority of households. However, because we are interested in
child growth in the first 5 years of life – particularly the 12–23 month period – we treat
both rounds as repeated cross-sections rather than a panel.5 The combined rounds make up a
sample of 11,796 households (some surveyed twice), which includes 4268 pre-school children
aged 0–59 months. Height-for-age Z scores (HAZ), using the World Health Organization’s
global child growth reference standards (WHO, 2006), constitutes our primary outcome of
interest. As noted above, from 6 months to around 24 months growth faltering tends to be
particularly pronounced in developing country populations due to prolonged nutritional
deficiencies associated with inappropriate complementary feeding and repeated or chronic
infections (Victora et al., 2010). It is also common to define children as stunted if HAZ
falls below -2, though statistical epidemiologists have strongly argued against using
dichotomous dependent variables, as it unnecessarily discards valuable information and
reduces precision (Royston et al., 2006). However, we report stunting results as an
extension to our main HAZ results. In this paper our interest is in dairy production-dairy
consumption pathways, rather than dairy production-income/wealth pathways (in principle,
income from any source could improve diets). Our regression models therefore control for
household expenditure and wealth, but our dataset also allows us to examine whether dairy
consumption is likely to be the main mechanism linking cow ownership to child growth by
using additional data on children’s consumption of various foods as well as household data
on how different foods were obtained. In terms of the former we primarily focus on
children’s consumption of dairy products in the past 24 h, defined as a dichotomous
indicator. To help rule more generic income-based pathways we also use a dietary diversity
score (0–6 food groups) that excludes dairy, as well as estimates of children’s total
calorie consumption (excluding breastmilk). Our expectation is that dairy production
influences dairy consumption, but not non-dairy dietary diversification or total calorie
intake. We can also explore how households sourced different foods since the BIHS asks
respondents to estimate the proportion of each food provided through market purchases,
provided by other sources, or provided by home production. We also note that, in
principle, these consumption data might also be used to examine the impacts of dairy
consumption on child growth. However, a critically important limitation of consumption
data is that they are based on short recall periods (24-hour or weekly recall), meaning
that they are potentially quite poor indicators of regular consumption of milk in the past
12 months or more (Thorne-Lyman et al., 2014). This measurement problem with short-recall
consumption suggests that longer recall questions on milk production may be a much better
indicator of regular access to dairy products in settings where markets for perishable
products are highly imperfect. However, since long-recall production quantity indicators
also suffer from bias we use a simpler dichotomous indicator of whether or not milk was
produced in the last 12 months – along with cow ownership - to define our treatment,
placebo and control groups. Clearly these groups are not the result of random assignment,
although we can use multivariate regressions to reduce the biases of confounding factors
that influence cow ownership or lactation decisions. We first assess the determinants of
milk production, with the expectation that cattle herd size (female and males) is a key
observable driver that we can subsequently control for in our main HAZ regressions. We
then use multivariate reduced form regressions to control for a broader range of potential
confounding factors. In addition to dairy herd size, we were also concerned that cattle
ownership may simply reflect more generic livestock wealth, so we extensively control for
other forms of livestock (bullock/buffalo, goat, sheep, chicken, duck and other birds) and
aggregate livestock into an index of Tropical Livestock Units (TLU), which can be thought
of as a measure of aggregate livestock wealth. The remaining control variables are more
common to most nutrition specifications, and to estimation of health production functions,
such as Todd and Wolpin (2007) and Hoddinott et al. (2015). This includes child
characteristics (sex, age, breastfeeding status), parental characteristics (age and
schooling), household characteristics (per capita monthly expenditure, the aggregate value
of 26 household assets, hectares of cultivable land owned, household toilet and water
access, access to electricity, exposure to NGO services) and several community
characteristics (distances to the nearest weekly/periodic outdoor market, and to the
nearest town and to the nearest health centre). Our regressions also include fixed effects
for all 65 districts in which the BIHS was conducted. Clearly the main coefficient of
interest is that pertaining to the treatment group, which we interpret as the effect of
dairy availability on child growth net of any impacts of dairy production on other inputs
into the health production function, such as income, or changes in breastfeeding. However,
we also test for significant differences between the coefficients for treatment and
placebo, and whether the coefficient for placebo is significantly different from zero
(i.e. from the control, the omitted control group). A significant coefficient on placebo
would suggest that cattle ownership influence HAZ through channels other than dairy
consumption. A biological issue of paramount importance is the need to explore age-
specific variation in the sensitivity of children’s growth to exposure to dairy
production, an issue emphasized in Hoddinott et al. (2015). For the HAZ analysis we
primarily focus on children 6–23 months and 24–59 months, as well as smaller age
intervals. The biology of growth identified in Victora et al. (2010) suggests that most
growth faltering takes place in the 6–23 month window, so dairy consumption in this period
ought to be critical. We do report results for older children (24–59), although it is not
clear that our 12-month dairy production indicator should predict stronger growth because
of misclassification errors. That is, some 24–59 month children who may have consumed
dairy in the past 12 months (according to our indicator) may not have consumed dairy in
their critical 6–23 month window. In our extensions to the basic model we also examine two
indicators that were not collected for all households and would therefore entail sample
restrictions: maternal nutrition knowledge score and a maternal empowerment score based on
women’s control over and ownership of various agricultural assets. We use these indicators
as dependent variables to test whether dairy producing households are significantly more
likely to have mothers with better nutrition knowledge or greater empowerment. Here we
test the null hypotheses that the coefficient on treatment is equal to that of placebo and
control. Rejection of this null would cast doubt might suggest that part of the estimated
effects of milk production on HAZ pertains to greater nutrition knowledge or empowerment.
We also estimate alternative HAZ specification where production quantities of milk are
used in place of the dummy variable for any milk produced. This is not our preferred
indicator because of concerns over measurement error, related to the challenges of
accurately recalling production over a long period, but we nevertheless consider it a
useful alternative test.

<hs>  Descriptive statistics</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

Table 1 provides descriptive statistics for the key variables for a sample of children
0–23 months of age. Fig. 1 also reports a local polynomial smoother curve (LPOLY) of HAZ
scores against child age to reveal the dynamics of growth faltering in rural Bangladesh.
There are several broad inferences to be made from these results. First, the sample of
children is highly undernourished, consistent with other nationally representative surveys
of Bangladesh. Mean HAZ scores are −1.37, and one third of children are stunted (by age
two fully half are stunted). However, consistent with previous research (Victora et al.,
2010), most of the growth faltering in Bangladesh occurs in the 6–23 month window, as
shown by the red vertical lines in Fig. 1. This accelerated period of growth faltering
could partially be due to poor diets. Notably, the percentage of all children who consumed
dairy in the past 24 h is just 22%, which is particularly low given that in more developed
societies many children would consume milk on a daily basis. Consistent with low milk
consumption is the low ownership of milk producing cows (14%), while a further 8% own a
cow that has not produced milk in the past 12 months.

<hs>  Determinants of milk production</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The higher socioeconomic status of treatment might imply that any apparent benefits of
dairy production partially reflect the benefits of greater socioeconomic status. This
points to the importance of multivariate regression models saturated with a wide array of
controls, as well as the importance of placebo tests. However, we can also examine the
determinants of milk production across among households that own at least one cow
(treatment and placebo) to assess the relative importance of herd size versus other
socioeconomic indicators. On biological grounds one would expect milk production to be
strongly associated with herd size, including the number of both female animals and male
animals. Owning more female animals obviously reduces the risk that the herd as a whole
will not have produced any milk in the past 12 months. However, without male animals,
producers would need to either rent in bulls, or access artificial insemination services.
While the latter are common in Bangladesh, previous research points to poor farm
management practices reducing the success of artificial insemination services (see
footnote 3). Table 2 reports the results for those variables that statistically explain
whether or not a cow-owning household has produced milk in the past 12 months. With the
exception of maternal age, the only significant predictors of dairy production status are
indicators of herd size; coefficients on the range of other indicators of household
socioeconomic status are all insignificant, individually and jointly. The results suggest
that milk production status is non-linearly related to herd size: owning 2 dairy cows or 1
bullock greatly increases the probability of producing milk in the past year, but
additional animals do not much alter these probabilities. Fig. 2 explores the relationship
between herd size and annual milk production on the y-axis and the number of cows owned on
the x-axis. However, we plot a curve for households that own at least one bullock, as well
as those that do not, in order to examine interaction effects. The results reveal the
expected finding that owning just one cow with no bullock results in very low levels of
milk production because there is a high likelihood that this single cow may not have been
lactating at any time in the past 12 months. Owning more cows greatly improves milk
production. Moreover, the returns to owning one cow and at least one bullock are fairly
high, and not greatly increased by owning more cows.

<hs>  Associations between dairy production and dietary indicators</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Fig. 3 shows local polynomial smoother plots of the relationship between 24-hr dairy
consumption and child age, with 90% confidence intervals (CIs). We use 90% CIs in order to
implement a one sided test at the 5% level that treatment status is associated with higher
HAZ. Panel (i) compares treatment to placebo, while Panel (ii) compares treatment to
control. The 90% CIs do not overlap in either panel, indicating that treatment children
have significantly higher levels of dairy consumption compared to the placebo or control
groups throughout the 0–59 month age range. The magnitude of the difference between
treatment and placebo and control varies between 15–25 percentage points depending on the
age of the child. Table 3 examines this relationship in a multivariate regression model
with a full set of controls, but also looks at whether milk production has any impact on
non-dairy dietary diversity and child calorie intake. Results in Regression (1) suggest
that milk production leads to approximately a 14-point increase in milk consumption,
although some of the difference in milk consumption across groups observed in Fig. 3 is
likely driven by differences in socioeconomic status (household expenditure, maternal
education) across groups.6 Another striking result from Fig. 3 is that many children under
the age of 12 months consume cow’s milk, even though recommendations (albeit based more on
developed country samples) recommend milk consumption be initiated only at 12 months (FAO,
2013). Moreover, previous research using the same dataset suggests that children are often
given the lion’s share of a household’s milk supply in Bangladesh (Sununtnasuk and
Fiedler, 2017). Finally, Table 3 also examines whether there are systematic differences in
non-dairy dietary diversity across groups, as well as total calorie intake (exclusive of
breastmilk). We find no significant associations between treatment and these two dietary
indicators, although the placebo group has higher calorie intake than the treatment or
control groups. The lack of any impact on non-dairy dietary diversity suggests the results
may not be confounded by socioeconomic differences between groups (Hoddinott, Headey and
Dereje 2014). The lack of a significant impact on calories suggests that milk consumption
is not primarily operating through increasing a child’s overall calorie intake in this
context.

<hs>  Associations between dairy production and child growth</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Table 4 presents least squares regression results with a full set of control variables,
stratified by 6–23 months, 24–59 months, and then by series of overlapping 12-month age
brackets used to further corroborate the importance of milk in this 6–23 month window. The
most striking result is the large 0.52 standard deviation (SD) difference between
treatment and control children in the 6–23 month window; a difference which entirely
disappears in the 24–59 month window. The latter result is likely explained by the fact
that there may be low serial correlation between milk production in the past year and milk
production in earlier years, precisely because of variations in lactation cycles among
small-scale dairy producers. In columns (3) and (4) we see that the results are consistent
across the 6–17 month and 12–23 month windows, though column (4) shows a relatively large
but insignificant coefficient on the placebo group coefficient, while column (5) confirms
that the benefits of milk production are no longer apparent once we move above the 23
month threshold. We interpret this as evidence that milk consumption has its largest
impact in the first 1000 days; as the age range moves beyond ∼23 months the 12 month
recall becomes a more imprecise indicator of whether the child actually consumed milk in
the 6–23 month period. Further confirmation that the results are strongest in the 6–23
month period is provided by Wald tests of significant differences between the treatment
and placebo coefficients in the 6–23 month, 6–17 month and 12–23 month ranges. This
suggests that it is milk production, not cattle ownership per se, that yields sizeable
benefits for linear growth in early childhood.

<hs>  Extensions</hs>
  ~~~~~~~~~~

In addition to the results above we also engaged in a series of extensions designed to
explore some additional complexities in the associations examined above. We first tested
for differential impacts of treatment on boys and girls, but found no statistically
significant differences in results for the age ranges above. We also tested for
interactions between treatment status and maternal empowerment scores and maternal
nutritional knowledge on the grounds that these might be mediating factors, but all
interactions were insignificant. We also included empowerment scores and knowledge scores
as dependent variables to see if these might be potential confounding factors, but
treatment status had no significant impact on either variable (results available on
request). In Table 5 we used stunting status (HAZ<-2) as the dependent variable. Stunting
is a widely used public health measure, although using a dichotomous indicator rather than
a continuous indicator effectively discards information and is likely to reduce precision.
The pattern of results in Table 5 are very similar to those reported in Table 4, although
the Wald tests no longer report statistically significant differences across the treatment
and control groups (seemingly due to the expected increase in imprecision). That caveat
aside, the results imply that regular dairy consumption has strong impacts on stunting,
although treatment-control and treatment-placebo comparisons yield quite different
inferences. Among children 6–23 months the model predicts a 10.4-point reduction in
stunting relative to the control group. However, the placebo group also has a large,
negative but statistically insignificant coefficient that – interpreted literally – would
imply only a 2.4-point reduction in stunting from exposure to treatment. Among children
12–23 and 18–29 months the point estimates on treatment are even larger, implying 14 and
22-point reductions in the risk of stunting relative to control, and 8.4-point and
11.3-point reductions relative to the placebo group. Overall, then, these results for
stunting status are broadly similar to the HAZ results in Table 4, although it is no
longer possible to establish statistically significant differences between treatment and
placebo. An alternative to modelling a dichotomous indicator of whether the household
produced any milk is to specify the household’s estimate of the quantity of milk it
produced in the past 12 months, which we measure as the log of litres per child. OLS
coefficients estimates for this indicator are reported in Table 6. These coefficients are
significant in the 6–23 month and 12–23 month brackets, and marginally insignificant in
the 6–17 month bracket. In the 6–23 month range the coefficient implies that increasing
milk production by 10% would reduce stunting by 0.08 percentage points. The coefficients
are imprecisely estimated, however, and likely suffer from attenuation bias related to the
significant challenges that respondents have in accurately answering 12-month recall
questions. Overall, though, the results are broadly consistent with the results from Table
4.

<h>EXPLORING THE RELATIONSHIP BETWEEN DAIRY PRODUCTION AND BREASTFEEDING</h>
---------------------------------------------------------------------

One concern with the results reported in Fig. 2 is that many children in the treatment
group consume dairy at young ages (Fig. 3) when it may be harmful to the infant digestive
system (FAO, 2013), or may substitute for breastmilk, which has been linked with a range
of desirable health outcomes (PAHO/WHO, 2003). In this section we explore whether there
might be substitution between breastmilk and household supplies of dairy milk. Fig. 4
plots breastfeeding status by child age with comparisons between treatment and placebo
(Panel i) and treatment and control (Panel ii). The results show that, from birth to
around 8 months of age, dairy-producing households are significantly less likely to
breastfeed their children. Above this age range there is no significant difference in
breastfeeding rates. This suggests that access to dairy milk may have a negative spillover
on breastfeeding practices in the critically important 0–5 months age range when it is
strongly recommended for infants to be exclusively breastfed. In Table 7 we estimate a
linear probability model with current breastfeeding status as the dependent variable, with
the usual battery of control variables included to see whether the results in Fig. 4 are
robust to a multivariate model. This is indeed the case: children 0–11 months from
treatment households are around 21.7% less likely to be breastfed than children from
control households, and there is a similar statistically significant difference between
treatment and placebo. The evidence therefore suggests that easy access to dairy milk
greatly reduces the incentive for mothers to breastfeed.

<h>CONCLUSIONS</h>
-----------

Despite strong biological evidence on the links between dairy consumption and child
growth, and substantial empirical evidence from developed country populations,
surprisingly little research has documented the impacts of regular consumption of dairy
products on child growth in developing countries. Recent economic research has instead
examined associations between cattle ownership and child growth, but only looked at East
African populations. And to our knowledge none of this research has examined substitution
of dairy milk for breast milk. In this paper we examined these associations in Bangladesh
where we were able to distinguish between cows that produced milk in the past 12 months
and those that did not. This dichotomy served two purposes. First, by focusing more
specifically on herds that have actually produced milk our estimates may more closely
approximate the growth benefit of the latent variable of interest, the regular consumption
of dairy products. Second, “treating” children with cows that have not produced milk
offers a potentially meaningful placebo test. We find results broadly consistent with the
findings of East African settings. Similar to Hoddinott et al. (2015), we were able to
disaggregate results by age and show that the benefits of cattle ownership (or regular
supply of dairy products) emerges primarily in the 6–23 month critical window of child
growth. However, Hoddinott et al. (2015) find an estimated impact of owning at least one
cow of 0.21 standard deviations, without knowing whether the cow produced milk or not.
When we replicate that approach we find an impact of 0.35 standard deviations for owning
any cow (results available on request), whereas the results reported above suggest an
estimated impact of 0.52 SD for owning at least one cow that produced milk in the past 12
months. Hence the associations estimated in this paper are substantially larger and
partially pertain to the use of a better proxy for regular milk consumption. Our point
estimates are very similar in magnitude to those of Rawlins et al. (2014) from Rwanda, and
Kabunga et al. (2017) from Uganda, even though both of those studies focus on improved
(high-yielding) cattle varieties rather than ownership of any type of dairy cow. This
literature therefore corroborates existing evidence on the importance of cow’s milk for
linear growth, which mostly stems from more developed settings (Iannotti et al., 2013; de
Beer, 2012; Hoppe et al., 2006). Given that less than a quarter of rural Bangladeshi
children consumed dairy products over the previous 24 h, and that almost half of rural
Bangladeshi children are stunted, increasing dairy consumption among children and women of
childbearing age should be a central priority for nutritional strategies in Bangladesh.
The best means of doing so is unclear, however. With exceptionally high population
densities even in rural areas, Bangladesh has no clear comparative advantage in large-
scale dairy production and may ultimately need to rely more on milk powder imports, which
are still heavily taxed with a tariff of 25%. Additional constraints may be more cultural
in nature. Like many East Asian countries, Bangladesh has no strong tradition of milk
consumption. However, several East Asian countries, such as Thailand and Vietnam, have
been extremely successful in increasing dairy consumption through combinations of imports
and rapid growth in domestic production, as well as marketing campaigns and school feeding
programs aimed at increasing nutritional knowledge and consumer demand for dairy products
(FAO, 2008). However, our results also provide a further rationale for utilizing campaigns
aimed at improving nutritional knowledge; that there is a need to reduce the perceived
substitutability between dairy products and breastmilk.


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<ART>Household food group expenditure patterns are associated with child anthropometry at ages 5, 8 and 12 years in Ethiopia, India, Peru and Vietnam
================================================================================

Authors: Debbie L. Humphries, Kirk A. Dearden, Benjamin T. Crookston, Tassew Woldehanna, Mary E. Penny, Jere R. Behrman
DOI: 10.1016/j.ehb.2017.02.001
Year: 2017  |  Pages: 30-41
ASJC codes: 2001
Keywords: Child growth, Household food expenditures, Household food purchasing patterns, Longitudinal cohort study, Weight gain

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Population-level analysis of dietary influences on nutritional status is challenging in part due to limitations in dietary intake data. Household expenditure surveys, covering recent household expenditures and including key food groups, are routinely conducted in low- and middle-income countries. These data may help identify patterns of food expenditure that relate to child growth. Objectives We investigated the relationship between household food expenditures and child growth using factor analysis. Methods We used data on 6993 children from Ethiopia, India, Peru and Vietnam at ages 5, 8 and 12y from the Young Lives cohort. We compared associations between household food expenditures and child growth (height-for-age z scores, HAZ; body mass index-for-age z scores, BMI-Z) using total household food expenditures and the “household food group expenditure index” (HFGEI) extracted from household expenditures with factor analysis on the seven food groups in the child dietary diversity scale, controlling for total food expenditures, child dietary diversity, data collection round, rural/urban residence and child sex. We used the HFGEI to capture households’ allocations of their finances across food groups in the context of local food pricing, availability and pReferences Results The HFGEI was associated with significant increases in child HAZ in Ethiopia (0.07), India (0.14), and Vietnam (0.07) after adjusting for all control variables. Total food expenditures remained significantly associated with increases in BMI-Z for India (0.15), Peru (0.11) and Vietnam (0.06) after adjusting for study round, HFGEI, dietary diversity, rural residence, and whether the child was female. Dietary diversity was inversely associated with BMI-Z in India and Peru. Mean dietary diversity increased from age 5y to 8y and decreased from age 8y to 12y in all countries. Conclusion Household food expenditure data provide insights into household food purchasing patterns that significantly predict HAZ and BMI-Z. Including food expenditure patterns data in analyses may yield important information about child nutritional status and linear growth.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Globally, 165 million children are stunted and 50 million children are wasted (Black et
al., 2013a). Stunted and wasted children suffer short- and long-term consequences (Walker
et al., 2005; Crookston et al., 2011; Victora et al., 2008; Behrman, 2014); therefore,
improving children’s nutrition is a global priority (United Nations, 2014; United Nations,
2016). Food intake is one of the causes of undernutrition. It is difficult to identify
through population-level analyses what aspects of food intake drive poor nutritional
status, in part because information on influences on the food choices that determine
consumption is often lacking. Heterogeneities in food consumption may be considerable
across households because of variations in preferences, food prices, food availabilities
and resource constraints. Investigating patterns in food expenditures at the household
level may provide a novel tool for assessing child and household nutritional risk.
Furthermore, accurate quantitative measures of dietary intake are time-consuming to
obtain, and require extensive food composition databases and nutritional expertise for
data collection and analysis (Willett, 1998; Gibson, 2005; Magarey et al., 2011; Fiedler
et al., 2013). Additionally, when researchers, program planners and evaluators collect
data on foods and liquids consumed in the previous 24 h, this information may not reflect
usual intake (Sempos et al., 1985). Because policy makers lack access to information on
usual patterns of dietary intake, it is challenging to determine best approaches for
improving individuals’ consumption of food. Data on household food expenditures (defined
as market purchases, gifts and foods drawn from own production or stocks consumed by the
household) reflect periods longer than 24 h (often 2 weeks) and are consistent, for
example, with Living Measurement Surveys conducted by The World Bank and national
statistical bureaus (Long et al., 2007). Field workers collecting household expenditure
data need to be trained. Similarly, individuals who collect and analyze data using 24-h
recalls need specialist training. However, in contrast to use of expenditure data,
analysis of dietary intake data requires regular, time-consuming updates of food data
bases with information on food preparations, corrections for cooking, waste and portions
(Gibson, 2005). Additional advantages and disadvantages of 24-h recall data and
expenditure data are outlined in Box 1. Many governmental and non-governmental
organizations conduct household consumption and expenditure surveys (HCES) that include
information on how much households spend on key food groups. They conduct these surveys
every 3–5 years in more than 125 low- and middle-income countries (Fiedler et al., 2012a).
Several studies demonstrate significant relationships between nutrient intake based on
dietary intake and nutrient intake derived from food expenditures (Naska et al., 2001;
Jariseta et al., 2012) after converting food expenditure data to estimates of individual
dietary intake (Fiedler et al., 2012a). The HCES surveys are important sources of
information on family food choices. Some researchers have converted HCES data to estimates
of dietary intake to identify implications for nutritional policy and planning (Jariseta
et al., 2012; Fiedler et al., 2012b; Bermudez et al., 2012). One of the important benefits
of utilizing HCES data is the lower cost of data collection. According to one estimate,
the cost of collecting and analyzing 24-h recall data is estimated to be 75 times that of
utilizing HCES data on household food expenditures (Fiedler et al., 2013). We hypothesize
that household dietary patterns, as reflected in food expenditure data, are important
drivers of family and individual dietary quality which will be manifested in measures of
child growth. Household food expenditure surveys have been used to explore determinants of
child nutritional status (Bermudez et al., 2012; Campbell et al., 2010; Sari et al., 2010;
Torlesse et al., 2003; Mauludyani et al., 2014). Associations have been observed between
specific food expenditure patterns and nutritional status. For example, in Indonesia, Sari
and colleagues documented that higher household expenditures on non-grain and animal-
source foods reduced the risk of stunting among children ages 0–59 months (Sari et al.,
2010). In these studies, researchers used information on expenditures for specific food
groups and combinations of food groups, selecting those food groups that have been shown
most frequently to be associated with nutritional status. Data reduction approaches such
as factor analysis and principal components analysis (PCA) have been used by some
investigators to identify patterns in food consumption based on dietary intake data
(Becquey et al., 2010; Bedard et al., 2015; Devlin et al., 2012; Moskal, 2014; Pisa et
al., 2015). We extend the use of data reduction approaches to household food expenditures
to determine whether there are underlying drivers of food expenditure patterns that are
associated with child growth. Fig. 1 represents the conceptual framework guiding this
research. We posit that household characteristics (preferences, resources, demographics)
and community characteristics (food prices and availability, urbanization) underlie three
important indicators of food consumption: 1) allocation patterns of household expenditures
across food groups, 2) dietary diversity (an indicator of likelihood of achieving
necessary micronutrient intakes), and 3) total household food expenditures (an indicator
of dietary quantity). We test the hypotheses that each of these three is associated with
children’s nutritional status. In this study, we examine a cohort of children from four
diverse low- and middle-income countries (Ethiopia, India, Peru and Vietnam) using food
group expenditure data and a variety of analytic strategies. We characterize household
food group expenditure patterns and estimate their associations with children’s
nutritional status ((height-for-age (HAZ) and body mass index (BMI-Z)) during early and
middle childhood. Our analyses are innovative because 1) our data cover children from ages
5–12 years, 2) we assess the broad applicability of findings across four diverse settings,
and 3) we describe associations between food group expenditure patterns and children’s
nutritional status. This work contributes to the ongoing conversation about using HCES
data for nutrition policy (Fiedler et al., 2012a; Fiedler, 2013), while also exploring a
novel approach to identifying patterns in HCES data that is less expensive and less
dependent on assumptions than converting HCES expenditure data to estimates of individual
level dietary intake.

<hs>  Study design and participants</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We used data from the Young Lives (YL) study younger cohort, which is comprised of ∼8000
children in Ethiopia, India, Peru, and Vietnam. The YL study team recruited ∼2000 children
from each country in 2002 (round 1) at approximately 1y of age with subsequent data
collection at age 5y (round 2: 2006), age 8y (round 3: 2009) and age 12y (round 4: 2013).
YL used a multistage sampling design which was pro-poor, with the first stage consisting
of selection of 20 sentinel sites. In Ethiopia, the sampling universe included the most
food-insecure areas. In Peru, the richest 5% of districts were excluded from the sample.
While poor clusters were moderately oversampled, the final samples represented a variety
of social, geographic, and demographic groups. The sample in India consisted of households
from Andhra Pradesh and Telangana, while the three other countries used nationwide samples
(Humphries et al., 2015). Children’s ages at each round ranged from 6 to 18 months
(hereafter “1y”, round 1), 4.5 to 5.5 years (“5y”, round 2), 7.5 to 8.5 years (“8y”, round
3) and 11.5 to 12.5 y (“12y”, round 4). Sampling methods have been reported previously
(Humphries et al., 2015). Additional study methods are described elsewhere (Barnett,
2012), and are provided at http://www.younglives.org.uk (Young Lives., 2015). From age 1y
to age 12y, the YL country cohorts lost between 1.5% and 5.7% of participants to attrition
(Ethiopia 114/1999; India 81/2011; Peru 106/2052; Vietnam 36/2000). Household food
expenditures were collected starting with round 2; consequently, this study included data
from rounds 2, 3 and 4. Children were excluded from each round if they were missing
information on anthropometry, rural/urban residence or household food expenditures. Final
sample sizes for rounds 2–4, respectively, were: Ethiopia (1744, 1742, 1733); India (1804,
1806, 1801); Peru (1795, 1788, 1775), Vietnam (1788, 1754, 1684).

     <hss>Household food expenditures</hss>

        The respondent (usually the mother) was asked to report on consumption of between
        21 and 33 food categories in the previous two weeks. For each food group, the
        respondent estimated (a) total expenditure on all individual foods in that food
        group consumed in the previous 2 weeks; (b) value of gifts received or food paid
        in lieu of wages in that food group; and (c) value of own stores used in that food
        group (whether from the household’s own production, shop or stocks). We aligned
        food groups across rounds and across countries to generate 18 groups that were
        included in rounds 2, 3 and 4. We then aggregated food groups in two different
        ways in preparation for factor analyses. Approach 1: For food groups for which
        many households reported no expenditures, we aggregated groups into combinations
        of similar foods to make, for example, a fruit and vegetables group and an animal
        source foods group (meat, fish, eggs, and dairy). Approach 2: We aggregated food
        group expenditures to align with the seven food groups in the WHO child dietary
        diversity measure (World Health Organization Department of Child and Adolescent
        Health and Development et al., 2010). Based on the YL household census conducted
        as part of data collection, we generated the number of adult equivalents (AE) in
        the household (Glewwe and Twum-Baah, 1991) and converted food group expenditures
        to per AE values. We adjusted food expenditures independently in each country
        based on country-specific consumer price indices (Young Lives., 2015). These
        values were adjusted to 2006 local currency and adjusted again to facilitate
        international comparability using purchasing power parity conversions (Taylor,
        2002; Taylor and Sarno, 2004). We summed total food expenditures across food
        groups to give a total food expenditure per adult equivalent. We winsorized
        expenditures in each food group to address outliers (Reifman and Keyton, 2010) for
        each of the four countries, replacing values below the first percentile with the
        1st percentile, and replacing values above the 99th percentile with the 99th
        percentile. Ethiopia (15.5, 16.2, 17.4) had the lowest total food expenditures per
        adult equivalent at each time point, and Peru (41.1, 47.3, 55.3) had the highest
        (Table 1). Ethiopia was the only country with the preponderance of food
        expenditures in the whole cereals category (Table 1). Peru (10.56–15.48) and
        Vietnam (8.54–12.0) had similar median levels of expenditures on animal source
        foods (ASF). In Peru ASF expenditures included dairy, meat and fish and in Vietnam
        ASF expenditures were predominantly meat and fish. Median egg expenditures were
        similar in Peru and Vietnam, lower in India, and minimal in Ethiopia (Table 1).
        The median level of expenditures on ASF in India (3.64–4.23) was about a third of
        the Peru and Vietnam medians, and the median in Ethiopia (0.59–0.86) was less than
        a quarter of the Indian expenditures (Table 1). Median fruit and vegetable
        expenditures were highest in Vietnam (3.35–4.45), followed by Peru (2.39–4.41),
        India (2.60–3.71) and Ethiopia (0.42–0.56) (Table 1).

     <hss>Child anthropometry</hss>

        Field workers measured height using locally-made stadiometers with standing plates
        and moveable head boards accurate to 1 mm. We calculated HAZ using WHO 2006
        standards for children 0–59 months (de Onis et al., 2006) and WHO 2007 standards
        for older children (de Onis et al., 2007). Field workers measured weight using
        calibrated digital balances (Soehnle) with 100 g precision. We calculated body-
        mass-indices for age (BMI-Z) using WHO growth curves. All measurements were taken
        according to WHO guidelines (World Health Organization Department of Nutrition for
        Health and Development and Development, 2008; United Nations Department of
        Technical Co-operation for Development and Statistical Office, 1986). Birth dates
        were drawn from children’s health cards when available, and mothers’ reports
        otherwise. Our analyses focused on HAZ and BMI-Z as the standard indicators of
        malnutrition in children (Black et al., 2013b).

     <hss>Dietary diversity</hss>

        We assessed individual dietary diversity by summing the number of standard dietary
        diversity food groups that the child was reported to have eaten the previous day
        (World Health Organization Department of Child and Adolescent Health and
        Development et al., 2010). We combined food groups into the seven recommended
        categories at age 5 y, including (1) starches (cereals, roots and tubers), (2)
        meat (meat, fish), (3) eggs, (4) legumes and nuts, (5) dairy, (6) fruit and
        vegetables, and (7) fats and oils. At ages 8 y and 12 y, vitamin A rich fruits and
        vegetables were recorded as separate categories as in the adult version of dietary
        diversity.

     <hss>Control variables</hss>

        Other measures included round of data collection, sex of child, and rural/urban
        residence.

<hs>  Statistical methods</hs>
  ~~~~~~~~~~~~~~~~~~~

We used Stata (version 14.0, 2013. Stata Corp) for all analyses. Results were considered
statistically significant for p values < 0.05. We present associations between household
food expenditures, dietary diversity and child growth (HAZ, BMI-Z) using (a) total
household food expenditures and (b) factor analysis extracted from household expenditures
on the dietary diversity food groups, controlling for total food expenditures, round of
data collection, rural/urban residence and sex of child. Factor analysis: we pooled food
expenditures at ages 5y, 8y and 12y in each country then analyzed food expenditures at the
country level. We ran both factor analysis and PCA with one, two and three factors for
each country, with the upper limit of three factors based on scree plots and eigen values
>1.0. We assessed each PCA and factor solution for loading >0.40 for at least three food
groups on each component or factor. None of the PCA solutions in any of the four countries
met those criteria. The one-factor solution in all four countries met these requirements,
so we utilized the one-factor solution for this analysis. The one-factor solution
represents the latent driver of households’ allocations of their food finances across food
groups, and we refer to the latent variable as the ‘household food group expenditure
index’ (HFGEI), which represents food choices within the constraints of household
preferences, household resources, and local food pricing and availability. We used
multivariable ordinary least squares regressions for HAZ and BMI-Z to examine associations
between food expenditures and anthropometry.

<h>RESULTS</h>
-------

Mean HAZ increased from ages 5y to 12y in India (−1.65 to −1.45), Peru (−1.53 to −0.97)
and Vietnam (−1.35 to −1.06), although it remained constant for Ethiopia (−1.48 to −1.47)
(Table 2). BMI-Z decreased from ages 5y to 12y in Ethiopia (−0.62 to −1.82), India (−1.16
to −1.35) and Vietnam (−0.31 to −0.65). Mean HAZ was negative in all countries across all
rounds, and mean BMI-Z was negative across all rounds in all countries except Peru, where
mean BMI-Z ranged from 0.52 to 0.67 (Table 2). The percentages of individuals who lived in
rural areas remained relatively constant in Ethiopia (59–60%), India (72–74%) and Vietnam
(80–81%), although Peru experienced a decrease from 45% to 27% because of migration to
cities (Table 2). In all countries there was an increase in mean dietary diversity from
age 5y to age 8y, and a decrease from age 8y to age 12y (Table 2). Peru had the highest
dietary diversity at each round, and Ethiopia had the lowest. Five food groups loaded on
the first factor, HFGEI, in all of the countries (starches, fruit and vegetables, meat and
fish, eggs, and fats), contributing significantly to the common variance across all of the
food groups (Table 3). However, we found that relative loadings for each of the food
groups were quite different across countries. Correlations of HFGEI with food group
expenditures also varied across the four countries (Fig. 2). For example, the correlation
between meat and fish expenditures and HFGEI were lowest in India (0.54), slightly higher
in Ethiopia (0.57), and highest in Peru (0.76) and Vietnam (0.80). Households in the
lowest quartile of HFGEI in Ethiopia spent on average 57% of their food expenditures on
starches (Table 4). Adjusted expenditure values allow cross-country comparisons. Based on
mean percentages of total food expenditures on specific food groups, we present a picture
of how households allocate their food budget. Across all four countries, mean percentages
of food expenditures on meat and fish were lowest for households in the lowest quartile of
HFGEI, and highest in the highest quartile of HFGEI (Table 4). We observed the same
pattern for fruit and vegetable expenditures for Peru and Vietnam, although in Ethiopia
and India there were minimal changes in percentage expenditures on fruit and vegetables
across the four quartiles of HFGEI (Table 4). Our findings suggest that total food
expenditures were positively associated with HAZ (p < 0.05) and BMI-Z (p < 0.05) in all
four countries after adjusting for study round, rural residence, and whether the child was
female (Table 5). With adjustments for dietary diversity and HFGEI, total food
expenditures were no longer a significant predictor of HAZ in Ethiopia and India. HFGEI
was associated with significant increases in child HAZ in Ethiopia, India, and Vietnam
with adjustments for data collection round, total food expenditures, dietary diversity,
rural residence and whether the child was female (Table 5). In the fully-adjusted models
that included study round, HFGEI, dietary diversity, rural residence, and whether the
child was female, total food expenditures remained significantly associated with BMI-Z in
India, Peru and Vietnam. Dietary diversity was inversely associated with BMI-Z in India
and Peru; namely a higher diversity score was associated with lower BMI-Z. Coefficients
for both countries were essentially the same (−0.048 for India and −0.047 for Peru) as
were p values (0.04 and <0.01). It is important to note that mean BMI-Z in India was
negative at all three ages, and mean BMI-Z in Peru was positive. Total food expenditures
were not significantly associated with BMI-Z in Ethiopia. In Peru, the only country with a
positive mean BMI-Z, there was a significant positive association between total food
expenditures and BMI-Z.

<h>DISCUSSION</h>
----------

We examined data from Young Lives, a cohort of children from Ethiopia, India, Peru and
Vietnam, spanning three ages (5, 8 and 12 yrs), to assess whether total food expenditures
(dietary quantity), dietary diversity (dietary quality), and household food group
expenditure patterns were associated with measures of undernutrition. We found that total
food expenditures were positively associated with HAZ (p < 0.05) and BMI-Z (p < 0.05) in
all four countries with adjustments for study round, rural residence, and whether the
child was female. Similar to other studies (Campbell et al., 2010; Sari et al., 2010;
Torlesse et al., 2003; Mauludyani et al., 2014; Rosinger et al., 2013), we found
associations between specific food expenditure patterns and nutritional status. For
example, Rosinger and colleagues (Rosinger et al., 2013) note that in a nomadic Amazonian
population, men (but not women) living in households with high monetary expenditures on
market foods (top third) had significantly higher BMI, weight, percentage body fat, and
probability of being overweight or obese. However, their study focused on adults, not
children. A recent analysis of household food expenditures and inflation in Mozambique
during 2008/2009 (Arndt et al., 2016) found higher rates of acute child malnutrition
(lower weight-for-age z scores, WAZ), in periods with higher quarterly rates of inflation.
When we included dietary diversity and the HFGEI in multivariate HAZ models, total food
expenditures were not significant predictors of HAZ in Ethiopia and India. According to
these results, how households allocate expenditures across food groups, may be a more
important driver of child linear growth than total food expenditures, at least for
Ethiopia and India. In multivariate BMI-Z models that included study round, HFGEI, dietary
diversity, rural residence, and whether the child was female, total food expenditures
remained significantly positively associated with BMI-Z in India, Peru and Vietnam. We
found that dietary diversity was inversely associated with BMI-Z in India and Peru. In
Peru, where mean BMI-Z is positive, the inverse relationship suggests that higher dietary
diversity is associated with a lower risk of higher BMI-Z, and potential overweight. In
India, where mean BMI-Z is negative, the inverse association between dietary diversity and
BMI-Z is more challenging to interpret. Previous analysis by this team found that dietary
diversity was not a significant mediator between food security and child anthropometry in
India (Humphries et al., 2015), although another recent study concluded that poor dietary
diversity is an important predictor of chronic undernutrition in India (Corsi et al.,
2016). The HFGEI was associated with significant increases in child HAZ in Ethiopia,
India, and Vietnam with adjustments for data collection round, total food expenditures,
dietary diversity, rural residence and whether the child was female. All countries showed
an increase in mean dietary diversity from age 5y to age 8y, which is likely an artifact
of the addition of one additional food group (vitamin A rich fruits and vegetables) at age
8y, and a decrease from age 8y to age 12y with the same number of food groups in those two
rounds. Five food groups loaded on HFGEI in all countries (starches, fruit and vegetables,
meat and fish, eggs, and fats), contributing significantly to the common variance across
all of the food groups, though relative loadings for each of the food groups were quite
different. While a number of researchers (Becquey et al., 2010; Bedard et al., 2015;
Devlin et al., 2012) have used factor analysis, PCA, and other approaches to identify
groups of foods based on dietary intake data, use of household food expenditure data is
less common (Campbell et al., 2010; Sari et al., 2010; Torlesse et al., 2003). In their
examination of the relationship between food expenditures and nutritional status, Rosinger
and colleagues identified five categories of market foods in a nomadic Amazonian
population. These foods are known to reflect the nutrition transition and included dairy,
oils, market meats, refined carbohydrates, and sweets. However, Rosinger et al. (Rosinger
et al., 2013) did not conduct factor analysis but rather summed total expenditures for
each food group. In contrast, Fan and colleagues (Fan et al., 2007) found eight clusters
of food expenditures ranging from “balanced” meals eaten largely at home to “fast food”
and “full service” meals consumed outside the household.

<h>LIMITATIONS</h>
-----------

Our study had several limitations. The intra-household allocation of food is unspecified,
so we do not know the relationship between household food expenditures and food
consumption of individual children. YL obtained information on child dietary diversity by
asking the mother or caregiver at ages 5y and 8y, and by asking the child directly at 12y.
In order to fully interpret the relationship between maternal vs. self-reported dietary
diversity for children we need to better understand patterns of dietary diversity as
children age. This study focuses primarily on current food consumption as a predictor of
child growth, although extensive literature (Dangour et al., 2013), including several
recent studies, have noted the importance of non-food influences on child height (Griffen,
2016; Krishna et al., 2016; Puentes et al., 2016; Dearden, et al. 2017). As noted
previously, the challenges associated with using dietary intake data are numerous and
include the importance of research staff with dietary data expertise, substantial
interview time, the difficulty of capturing such information, and complex analytic
methods. The conversion of food expenditure data into estimates of nutrient intake
requires details about food items purchased, local and seasonal costs and regularly
updated country-specific tables of food composition. In addition, assumptions regarding
intra-household food distribution are required. Use of food expenditure data as an
indicator of latent household food group expenditure patterns is simpler, though still
requiring assumptions about intra-household distribution, and our study indicates that
this measure provides insight into dietary patterns that are associated with child growth.
Importantly, food choice patterns may reflect a modifiable component of household
behavior, which could be addressed through behavior-change or market price interventions.

<h>CONCLUSIONS</h>
-----------

In this study, we 1) provide a new way to consider food preferences, relative prices and
availabilities by observing household food group expenditure patterns that are relevant
for nutritional status, 2) contribute to the literature on how household dietary quantity
and quality predict undernutrition, and 3) demonstrate the utility of food group
expenditure data as an indicator of potential nutrition risk. We used factor analysis to
identify an underlying pattern of consumption across food groups that is related to child
growth. Factor analysis and other data reduction techniques may add important information
over and above what is provided by total food expenditures alone (as reflected in their
significance in our estimates). This is useful because although disaggregated expenditure
data may be an important proxy of the types of foods households consume, in the aggregate,
their complexity may pose a challenge for policy makers, program planners, and managers
seeking to understand associations between food expenditures and children’s nutritional
status. This is particularly important because household expenditure surveys are routinely
conducted in many low- and middle-income countries. These surveys provide an important but
often neglected source of information about how much money households allocate to food,
which foods they prioritize, and whether such prioritization provides a diversity of
healthy foods. Thus, household expenditure surveys may also shed light on children’s
growth. More studies, especially those that are longitudinal in nature, are needed to
validate our findings and further explore changes in dietary diversity as children age. We
intend to continue examining Young Lives data to explore potential longitudinal effects,
sibling effects, and the relationship of HFGEI to other household characteristics such as
parental schooling attainment. In summary, our study has shown the potential for using
disaggregated household food expenditure data to explore patterns of household food
consumption as predictors of child growth. We report significant differences in these
patterns across four diverse low- and middle-income countries.

<h>CONFLICT OF INTEREST</h>
--------------------

Mary E. Penny has received research funding from the food industry for studies unrelated
to this research. The other authors declare no conflict of interest.

<h>FUNDING</h>
-------

This study is based on research funded by the Bill & Melinda Gates Foundation (Global
Health Grant OPP1032713), Eunice Shriver Kennedy National Institute of Child Health and
Development (Grant R01 HD070993) and Grand Challenges Canada (Grant 0072-03). The study
uses data from Young Lives, a 15-year survey investigating the changing nature of
childhood poverty in Ethiopia, India (Andhra Pradesh and Telangana), Peru and Vietnam
(www.younglives.org.uk). Young Lives is core-funded by the UK Department for International
Development (DFID) and was co-funded from 2010 to 2014 by the Netherlands Ministry of
Foreign Affairs. The authors are responsible for all the findings and conclusions: they do
not necessarily reflect positions or policies of the Bill & Melinda Gates Foundation, the
Eunice Shriver Kennedy National Institute of Child Health and Development, Grand
Challenges Canada, Young Lives, DFID or other funders.

<h>ETHICAL REVIEW</h>
--------------

The University of Oxford Ethics Committee and the Peruvian Instituto de Investigación
Nutricional IRB approved YL study protocols. Approval for these analyses was obtained from
the University of Pennsylvania. Written parental consent was obtained at the beginning of
the study and confirmed verbally at each round. Assent was obtained from children.


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  [38] Christopher T. Sempos, Nancy E. Johnson, Everett L. Smith, Catherine Gilligan. Effects of intraindividual and interindividual variation in repeated dietary records. doi:10.1093/oxfordjournals.aje.a113974
  [39] Mark P. Taylor, Lucio Sarno. International real interest rate differentials, purchasing power parity and the behaviour of real exchange rates: The resolution of a conundrum. doi:10.1002/ijfe.232
  [40] Alan M. Taylor. A century of purchasing-power parity. doi:10.1162/003465302317331973
  [41] Harriet Torlesse, Lynnda Kiess, Martin W. Bloem. Association of household rice expenditure with child nutritional status indicates a role for macroeconomic food policy in combating malnutrition
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  [46] Susan P. Walker, Susan M. Chang, Christine A. Powell, Sally M. Grantham-McGregor. Effects of early childhood psychosocial stimulation and nutritional supplementation on cognition and education in growth-stunted Jamaican children: Prospective cohort study. doi:10.1016/S0140-6736(05)67574-5
  [47] Walter C. Willett. Nutritional Epidemiology. doi:10.1093/acprof:oso/9780195122978.001.0001
<ART>Information acquisition, price informativeness, and welfare
===========================================================

Authors: Rohit Rahi, Jean Pierre Zigrand
DOI: 10.1016/j.jet.2018.07.007
Year: 2018  |  Pages: 558-593
ASJC codes: 2002
Keywords: Heterogeneous valuations, Information acquisition, Learning externalities, Welfare

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We consider the market for a risky asset with heterogeneous valuations. Private information that agents have about their own valuation is reflected in the equilibrium price. We study the learning externalities that arise in this setting, and in particular their implications for price informativeness and welfare. When private signals are noisy, so that agents rely more on the information conveyed by prices, discouraging information gathering may be Pareto improving. Complementarities in information acquisition can lead to multiple equilibria.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

We study the market for a risky asset for which agents have interdependent private
valuations. Heterogeneous valuations may arise for various reasons. For example, agents
may differ with respect to the uses they have for the asset, their liquidity needs, their
investment opportunities, or the regulatory constraints they face. Diversity in valuations
can be thought of as an indirect way to capture idiosyncratic preference or endowment
shocks.1 It can also be interpreted in purely behavioral terms – for example, agents could
“agree to disagree” about the distribution of the asset payoff, or a subset of traders
could be subject to psychological biases or misperceptions. Each trader is uncertain about
his own valuation, and has the opportunity to acquire private information about it prior
to trade. Equilibrium prices reflect some of this information. We use a standard
competitive rational expectations setup, with Gaussian shocks and constant absolute risk
aversion, that nests the classical models of Grossman and Stiglitz (1980) and Hellwig
(1980). Essentially the only difference with respect to the classical framework is that we
allow agents' valuations to be imperfectly correlated. This gives us a tractable model of
partial revelation without resorting to exogenous noise trade, with a unique linear
equilibrium price function for any allocation of private information. The model highlights
the role played by learning externalities in determining the information content of prices
and the welfare of market participants. The welfare analysis is complicated by the fact
that price informativeness is a multidimensional object in an economy with heterogenous
valuations and, moreover, there is no unambiguous link between price informativeness for a
given type and the welfare of that type. Agents can make better portfolio decisions if
prices are more informative about their valuation. But more informative prices are also
closer to their true valuation, reducing profitable trading opportunities. We find that
increasing the cost of information acquisition for agents of the highest cost type leads
to a reduction in the proportion of these agents who acquire information, lowering price
informativeness for them and improving their welfare. Price informativeness for other
types is higher, on the other hand, while the effect on their welfare depends on how
precise their private information is. When their private signals are noisy, so that they
have more to gain from learning from prices, they are better off. This is the case in
which discouraging information acquisition by the highest cost type makes all types better
off. Notice that it is precisely when prices have an important role to play in aggregating
and transmitting private information that curtailing the collection of private information
(by a subset of agents) is Pareto improving. A more general takeaway is that private
information collection can impact different groups of agents differently, both in terms of
the information conveyed by prices and welfare. Across-type complementarities, wherein
information gathering by one type interferes with learning from prices by other types, are
an important ingredient of our welfare result. Within-type complementarities play no role
here, but are crucial when we consider equilibrium multiplicity. It can turn out that
there is an equilibrium in which no agent of type i (for some i) acquires information and
another equilibrium in which all of these agents do. In fact, in the equilibrium in which
no type i agent is informed, prices are more informative for all types, including type i.
Both across-type and within-type complementarities are at play here.

<hs>  Related literature</hs>
  ~~~~~~~~~~~~~~~~~~

Vives (2014) studies a competitive rational expectations equilibrium model with private
valuations. As in our paper, there is no equilibrium with a high correlation of types, and
when an equilibrium does exist the price function is partially revealing. However, price
informativeness does not depend on the mass of informed agents (as long as this mass is
positive) – the price reveals the average type of all agents regardless of how many are
informed. This in turn implies that the information acquisition decisions of agents are
independent. Our stochastic environment shares some features with that of Rostek and
Weretka (2012, 2015), insofar as they allow heterogeneity in the correlations between the
private valuations of traders. They impose an “equicommonality” assumption, namely that
the average correlation between the valuation of a trader and those of the remaining
traders is the same for all traders. We do not impose any restriction on the correlation
structure for our results on the characterization of equilibrium and price informativeness
with exogenous private information (though we do impose symmetry in our analysis of
information acquisition). The aims of the Rostek–Weretka papers are different from ours –
they study the effect of an exogenous increase in the number of traders on price
informativeness (which, in contrast to our setting, is the same for all traders) and on
market power. Our framework generalizes the models of Grossman and Stiglitz (1980) and
Hellwig (1980), as well as several later extensions of these models. We go beyond this
literature in looking at information acquisition by different groups of traders, and
analyzing the learning externalities that arise both within and across groups. While the
social value of a public signal in a symmetric information economy has been the subject of
a voluminous literature going back to Hirshleifer (1971) (see Gottardi and Rahi, 2014 and
the references cited therein), not much research has been done on the welfare properties
of private information production when prices reflect some of this information. In
particular, the literature gives little guidance on the circumstances in which policies
that affect private information collection can improve market outcomes in a rational
expectations economy. In Vives (2014), information acquisition is socially efficient
provided the marginal cost of information is sufficiently low. This efficiency result is
not surprising given that there are no learning externalities in this model. Allen (1984)
shows that imposing a tax on information gathering in a variant of the Grossman–Stiglitz
model can make all agents better off. But the welfare analysis is compromised by the
presence of noise traders.2 In fact, most of the rational expectations literature relies
on exogenous noise trade and hence does not provide a suitable framework for welfare
analysis. Usually a proxy for welfare is employed, such as price informativeness, price
volatility or some measure of liquidity. There are a few papers that feature fully
optimizing traders but, with the exception of Vives (2014) cited above, they do not
address the question of the optimality of the equilibrium allocation of private
information. There is a large literature on complementarities in information gathering.
The closest to the present paper are competitive models in which these complementarities
arise because prices become less informative as more agents acquire information.3 Stein
(1987) provides an early example of the entry of informed speculators reducing price
informativeness for existing traders, in a setting where agents seek to forecast shocks to
the supply of the underlying in a futures market. In an environment closer to that of
Grossman and Stiglitz (1980), but with different assumptions on preferences and
distributions, Barlevy and Veronesi (2008) find that a complementarity can arise because
the asset payoff and noise trader demand are negatively correlated. Their mechanism has a
similar flavor to our within-type complementarity which is due to a negative correlation
between the valuations of traders from different groups. Price informativeness can be
decreasing in the incidence of informed trading in Ganguli and Yang (2009) and Manzano and
Vives (2011) because agents have access to two sources of information (about the asset
payoff and the asset supply), in Goldstein et al. (2014) because agents with different
trading opportunities in segmented markets may trade on the same information in opposite
directions, and in Breon-Drish (2012) due to non-normality of shocks. Relative to this
literature, our model admits a more pronounced multiplicity of equilibria, including
equilibria in which agents who collect information have a higher cost of information
acquisition than those who do not, in an otherwise symmetric economy. The paper is
organized as follows. We describe the economy in Section 2. In Sections 3–5 we take the
information acquisition decisions of agents as given. We characterize the unique linear
equilibrium price function in Section 3. Then, in Section 4, we provide several examples
in which this characterization can be employed. In Section 5 we analyze the information
content of the price for each type. We endogenize information acquisition in Section 6,
and discuss learning externalities within and across types. Section 7 is devoted to
welfare and Section 8 to equilibrium multiplicity. Section 9 concludes. Most of the proofs
are in the appendices.

<h>THE EQUILIBRIUM PRICE FUNCTION</h>
------------------------------

Optimal portfolios Equilibrium price function

<h>EXAMPLES</h>
--------

Grossman–Stiglitz Grossman–Stiglitz with optimizing liquidity traders Hellwig Multiple
hedgers This example is fully worked out in Appendix B; we provide the salient details
here.

<h>PRICE INFORMATIVENESS</h>
---------------------

Price informativeness

<h>ENDOGENOUS INFORMATION ACQUISITION</h>
----------------------------------

Utilities Utilities of informed vs uninformed Partial revelation An equilibrium vector λ
has at least two elements that are strictly positive. Price informativeness vs cost Lower
bound on ρ Ranking by price informativeness The incentive to acquire information depends
on the value of the common correlation coefficient ρ. Our next result characterizes the
values of ρ for which either all agents acquire information or none do. More precisely, in
the latter case, all agents have an incentive to free ride on the information gathering of
others, and hence there is no equilibrium. Information acquisition: polar cases λN-
equilibrium

<h>WELFARE</h>
-------

Welfare The learning externality for the other types goes in the opposite direction.
Information acquisition by type N agents interferes with learning from prices by agents of
types other than N (and this is true regardless of the value of ρ). This across-type
complementarity is responsible for the somewhat counterintuitive result that discouraging
information acquisition is Pareto improving precisely when prices have an important role
to play in information aggregation.

<h>COMPLEMENTARITY AND MULTIPLICITY</h>
--------------------------------

Multiple equilibria Multiple equilibria II The complementarity result in Goldstein et al.
(2014) has a similar flavor to ours: it is driven by a sufficiently strong hedging motive
that makes a subset of informed investors trade in the opposite direction to others who
only have a speculative motive. Another plausible scenario that can generate negatively
correlated valuations, described by Barlevy and Veronesi (2008), is one where some agents
have access to a private technology the returns on which are higher in good times, when
the asset fundamental is also high. These agents sell the asset in order to free up
resources for other projects.

<h>CONCLUDING REMARKS</h>
------------------

We study competitive rational expectations equilibria in an economy in which agents have
interdependent private valuations for the risky asset. For any given allocation of private
information, there is a unique linear equilibrium price function that takes a very simple
form. We characterize the endogenous distribution of private information when agents can
choose whether or not to pay for it. We highlight the role of learning externalities
within and across types of agents. When private signals are noisy and agents rely
primarily on the information transmitted by prices, raising the cost of information
collection for the highest cost type, and thereby curtailing their information gathering
activities, can make all types better off. When valuations across types are negatively
correlated, multiple equilibria can arise.


<h>REFERENCES</h>
----------

  [2] Snehal Banerjee, Brett Green. Signal or noise? Uncertainty and learning about whether other traders are informed. doi:10.1016/j.jfineco.2015.05.003
  [5] Jayant Vivek Ganguli, Liyan Yang. Complementarities, multiplicity, and supply information. doi:10.1162/JEEA.2009.7.1.90
  [6] Itay Goldstein, Yan Li, Liyan Yang. Speculation and hedging in segmented markets. doi:10.1093/rfs/hht059
  [7] Piero Gottardi, Rohit Rahi. Value of information in competitive economies with incomplete markets. doi:10.1111/iere.12041
  [9] Martin F. Hellwig. On the aggregation of information in competitive markets. doi:10.1016/0022-0531(80)90056-3
  [11] Carolina Manzano, Xavier Vives. Public and private learning from prices, strategic substitutability and complementarity, and equilibrium multiplicity. doi:10.1016/j.jmateco.2010.12.011
  [13] Brock Mendel, Andrei Shleifer. Chasing noise. doi:10.1016/j.jfineco.2011.02.018
  [14] Joel Peress. Learning from stock prices and economic growth. doi:10.1093/rfs/hhu021
  [15] Rohit Rahi. Adverse Selection and Security Design. doi:10.2307/2297853
  [16] Marzena Rostek, Marek Weretka. Price Inference in Small Markets. doi:10.3982/ECTA9573
  [17] Marzena Rostek, Marek Weretka. Information and strategic behavior. doi:10.1016/j.jet.2014.12.005
  [19] Xavier Vives. On the possibility of informationally efficient markets. doi:10.1111/jeea.12107
<ART>Is treatment “intensity” associated with healthier lifestyle choices? An application of the dose response function
================================================================================

Authors: Eleonora Fichera, Richard Emsley, Matt Sutton
DOI: 10.1016/j.ehb.2016.09.001
Year: 2016  |  Pages: 149-163
ASJC codes: 2001
Keywords: Dose-response function, Health behaviours, Non-linear dynamic models

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Healthy lifestyle choices and doctor consultations can be substitutes or complements in the health production function. In this paper we consider the relation between the number of doctor consultations and the frequency of patient physical activity. We use a novel application of the Dose-Response Function model proposed by Hirano and Imbens (2004) to deal with treatment endogeneity under the no unmeasured confounding assumption. Our application takes account of unobserved heterogeneity and uses dynamic non-linear models for the treatment and outcome variables of interest. Using seven waves of the British Household Panel Survey, we find that higher treatment intensity and frequency of physical activity are inversely related. We show that accounting for both treatment selection and unobserved heterogeneity halves the size of this relationship. An additional doctor consultation is associated with a 0.5 percentage point reduction in the probability of undertaking vigorous physical activity. Our results hold for a sub-sample visiting the doctor for health check-ups, and are shown to be robust using instrumental variables.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Within the World Health Organisation (WHO) European Region, almost 77 percent of the
disease burden is due to five major non-communicable diseases (NCD): diabetes,
cardiovascular diseases, cancer, chronic respiratory diseases and mental disorders.
Amongst its nine global targets to combat these diseases, the WHO has included a reduction
of physical inactivity and tobacco consumption, and an increase in treatment and
prevention of NCD by primary care doctors (World Health Organization, 2014). There is a
wide range of activities that primary care doctors can undertake in treating and
preventing NCD, including testing, prescribing and providing lifestyle advice to their
patients. A large literature has investigated the determinants of lifestyle behaviours and
contacts with primary care doctors (see for example, Manning et al., 1991; Kenkel, 2000;
Chaloupka and Warner, 2000; Cawley and Ruhm, 2011; Fernandez-Olano et al., 2006; Morris et
al., 2005). Both forms of health investments have common determinants, including socio-
economic and demographic factors, preferences, social networks and information. However,
little is known about the interaction between these investments. Our aim is to bring
together the literature on the determinants of lifestyle behaviours and healthcare
utilisation by examining the association between contacts with primary care doctors and
healthy lifestyle choices. There is a substantial literature showing that health status is
positively affected by the supply of doctors (see for example, Aakvik and Holmảs, 2006;
Auster et al., 1969; Gravelle et al., 2008; Or et al., 2005; Robst, 2001; Robst and
Graham, 1997). Evidence from the U.S., U.K., Norway and a cross-section of OECD countries
shows that increasing the number of doctors per capita decreases mortality rates and
improves health-related quality of life. In a Becker-type economic framework, the effect
of contacts with doctors on healthy lifestyle choices is ambiguous (Becker, 2007).
Individuals invest in their health to equate marginal utility of this investment with its
marginal cost. However, there is a trade-off between current costs of healthy lifestyle
behaviours (e.g. diverting time and resources away from other activities) and future
increased life expectancy. In an application of this model Kaestner et al. (2014)
identified two offsetting effects that are applicable to the present study. On the one
hand, there is a “competing risk of death effect” as more contacts with doctors might
increase the quantity and productivity of health investments which in turn increase life
expectancy and the benefit of investments in health. This leads to a positive association
between contacts with doctors and healthy lifestyle choices. On the other hand, Kaestner
et al. (2014) pointed out that a “technological substitution effect” might occur if
healthy lifestyle choices and contacts with doctors are substitutes in the health
production function. This leads to a negative association between contacts with doctors
and healthy lifestyle choices because more doctor contacts lower the marginal benefit of
other health investments. Although the direction of this association could have important
implications for policies that aim to increase access to health care professionals, only
one paper has explicitly investigated this empirical question. Schneider and Ulrich (2008)
used two waves of the German Socio-Economic Panel Study (GSOEP) to examine the relation
between a patient’s health-related behaviour and the probability of visiting a doctor.
Patients’ health-related behaviours were measured by an indicator that took a value of one
if the respondent was smoking and overweight. They used a recursive bivariate probit model
with the exclusion restriction that stress directly affects patients’ health-related
behaviour and does not directly affect visits to the doctor. As patients who are
overweight and smoke were more likely to visit the doctor, they found evidence of
substitutability between visits to the doctor and healthy lifestyle choices. Doctors can
affect patients’ health behaviours by providing lifestyle advice and treatment. Whilst we
would expect healthy lifestyle behaviours and lifestyle advice to be either complements or
independent of each other, treatment and health behaviours could be substitutes,
complements or independent of each other. The only three papers investigating this
relationship focused on different target populations and treatment regimens, and found
mixed results. Kaestner et al. (2014) used the Framingham Heart Study spanning between
1983 and 2001 to examine the relationship between the introduction and widespread
diffusion of statins and health behaviours. They found evidence that statin use is a
substitute for healthy diet with a particularly large increase in female obesity (33% of
the mean). They also found evidence of an increase in moderate alcohol drinking of about
15% of the mean and a decrease in sedentary activity among men. Using pooled cross-
sectional data from the Health Survey for England, Fichera and Sutton (2011) found that
prescription of lipid-lowering drugs complemented quitting smoking behaviour in patients
with cardiovascular diseases, but smoking cessation advice was not effective in reducing
smoking. Fichera et al. (2014) used a unique linkage between three waves of the English
Longitudinal Study of Ageing and practice-level data on the volume of treatments delivered
by doctors. They decomposed doctors’ effort into an element induced by the payment system
and a discretionary element, using an exogenous change in doctors’ remuneration that led
them to increase rates of prescription and disease control. They found that increases in
the rates of disease control decreased patients’ cigarette consumption. In this paper we
examine the association between the “intensity” of treatment and the level of effort that
individuals exert in protecting their own health. We measure treatment intensity as the
number of contacts with a primary care doctor and individuals’ health behaviours as the
frequency of their physical activity, their smoking and alcohol consumption in seven waves
of the British Household Panel Survey. This is a new empirical application of the relation
between treatment and healthy lifestyle choices as Kaestner et al. (2014), Fichera and
Sutton (2011) and Schneider and Ulrich (2008) did not examine the intensity effect of
treatment and Fichera et al. (2014) could only focus on practice-level treatment rates.
This is the first methodological application combining the continuous treatment approach
with dynamic panel data models. Identification is provided by comparing individuals with
different numbers of contacts with the doctor, but the same predicted “intensity” of
contacts based on their personal characteristics. The dose-response function uses the GPS
to capture the confounders that affect both visits to the doctor and healthy lifestyle
choices. It controls for confounding by (complex functions of) observable factors but does
not deal with unobserved confounding. We test the robustness of the results to this
limitation using fixed effects models and instrumental variables. The rest of the paper is
structured as follows. Section 2 describes the data and the summary statistics. Details of
our econometric methodology are examined in Section 3. Section 4 discusses the results.
Section 5 concludes.

<hs>  The British Household Panel Survey (BHPS)</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The BHPS is an annual survey of each adult (16 years of age and older) member of a
nationally representative sample of more than 5000 households, making a total of
approximately 10,000 individual interviews. In this survey individuals are asked “Since
[last 12 months], approximately how many times have you talked to, or visited a GP or
family doctor about your own health? Please do not include any visits to a hospital” with
the possible answers being: none; one or two times; three to five times; six to ten times;
and more than ten times. Individuals are not asked for reasons for their GP visits. In the
main analysis, we consider physical activity as the proxy for individuals’ investments in
their health. All individuals in the survey are asked about the frequency of their
physical activity in one of a succession of questions that ask about things people do in
their leisure time. As this question is asked every other year from 1996 to 2008, we
select seven of the 18 waves of the BHPS. From the question: “Please […] tell me how
frequently you: Play sport or go walking or swimming?” individuals can choose any of the
following: “At least once a week; At least once a month; Several times a year; Once a year
or less; Never/almost never”. We define physical activity in increasing level of
frequency, or effort. We also consider, as supplementary analysis, smoking and alcohol
consumption. Smoking is measured as the average number of cigarettes per day and alcohol
drinking is a four scale variable (from drinking at least once a week (1) to once a year
or less (4)). We consider a number of dummies indicating whether the respondent is white,
black, Asian (Indian, Pakistani, Bangladeshi or Chinese) or other ethnic background. A set
of dummy variables is included to indicate whether the respondent has obtained a
university degree, a high school diploma (the U.K. A-level or O-level), the Higher
National Diploma, a semi-professional qualification in the U.K or no qualification at all.
We consider the number of children under the age of two years in the household. We
dichotomise employment status to indicate whether the respondent is employed (either be
employee or self-employed) as opposed to retired, unemployed, on maternity leave or on
other employment status. We have taken the natural logarithm of the equivalised value of
household monthly income and deflated it by the consumer price index with 1995 as base
year. We also considered the number of rooms in the house as an indicator of wealth. A set
of dummy variables is included indicating the geographical region of the UK in which the
respondent lives. Respondents are asked to identify the physical health problems and
disabilities they are currently suffering from a list of 15 physical health conditions. We
group these conditions in an homogenous set of eight dummies: musculoskeletal (e.g. arms,
legs, feet and back problems); cardiovascular diseases (e.g. heart problems and high blood
pressure); diabetes; skin, head or sight problems; respiratory problems; stomach problems;
depression and other conditions. In addition to the type of conditions, we construct a
series of five dummies indicating the number of health conditions between 0 and two,
three, four, five and over six. In order to mitigate reverse causality both the number and
type of health conditions are measured at the first wave in which individuals are
interviewed. In supplementary analyses we focus on a subsample of individuals who have
visited the doctor at least once for preventive purposes. This is intended to alleviate
concerns that unobserved health conditions affect both the propensity to engage in
physical activity and doctor visits. Unfortunately, there is no longitudinal data in the
UK that asks patients for the reasons why they have visited the doctor. The English
Longitudinal Study of Ageing, like the BHPS, reports the type of conditions diagnosed by
the doctor and whether the respondent has visited the doctor, but does not contain the
number of doctor visits or the reason for visiting the doctor. The Health Survey for
England, a cross-sectional survey held since 1991, asks for the number of doctor visits
but not the reason for visiting the doctor. Therefore, we restrict one of our
supplementary analyses to BHPS respondents who have undergone at least one health check in
the last year. In a series of questions about which preventive health check-ups
respondents have undertaken, we select the National Health Service (NHS) check-ups that
are most likely done in a primary care practice. These are blood pressure measurement,
cholesterol measurement, cervical screening, breast screening and blood tests. In the
supplementary analysis, we restrict the sample to individuals who reported having had at
least one of these check-ups in the last year. Not all of the visits in this sample would
have been for preventive purposes, but this supplementary analysis is focused on a sub-set
of the full sample for which a greater proportion of their visits were for preventive
purposes. Nearly 2000 individuals per year (about 94% of the sample) reported having one
of these tests, leading to a combined sample of 11,736 observations. For our instrumental
variables analyses we generate two instruments: i) the number of times that the
individual’s spouse has visited to a doctor; and ii) the average number of consultations
with the doctor in the individual’s Local Authority District (LAD) of residence.

<hs>  Summary statistics</hs>
  ~~~~~~~~~~~~~~~~~~

In the main analysis we consider the population aged between 30 and 59 years because their
need for medical consultations and their health effort is expected to differ substantially
from the older population. Summary statistics are reported in Table 1. More than a quarter
of this population group have not been to the doctor in the past year. Approximately 37%
of respondents visited the doctor once or twice a year and 19% went to the doctor between
three and five times a year. More frequent visits to the doctor are rarer, with almost 9%
of people going to the doctor six to ten times a year and about 8% of people going more
than ten times a year. Whilst 48% of the sample reported playing sport, walking or
swimming at least once a week, 26% of people reported that they never or almost never
undertook these forms of physical activity. About 12% of people do these forms of physical
activity at least once a month and 9% several times a year. On average this sample has an
equivalised household monthly income of £679 and lives in a house containing five rooms.
About 78% of the population is either an employee or self-employed. Approximately 16% of
people report having at least a university degree and 51% report to have obtained a high
school diploma. The population aged between 30 and 59 years is relatively healthy, with
93% having at most two health conditions and only 2% of people reporting having six
conditions or more. About 16% of people report having a type of musculoskeletal problem
and 17% report skin, head or sight problems.

<h>ECONOMETRIC METHODOLOGY</h>
-----------------------

Our empirical strategy has two main features. Firstly, we predict the propensity score
from a (panel) grouped count data model to account for selection of the intensity of
treatment, as the number of visits to the doctor depends on individuals’ previous
behaviour and socioeconomic characteristics. Secondly, we also account for non-linearities
and persistency in the effort that individuals exert on their health investments with
panel data ordered probit models. Matching methods have been widely used in the programme
evaluation literature of the last two decades (see Augurkzy and Kluve, 2007 for an
overview). This is largely due to their ability to mimic experimental settings ex post. As
many observational studies involve non-binary treatments, recent literature has extended
propensity score methods to the cases of multi-valued treatments (Imbens, 2000; Lechner,
2001), and, more recently, continuous treatments (Behrman et al., 2004; Hirano and Imbens,
2004; Imai and van Dyk, 2004). Hirano and Imbens (2004) apply a generalisation of the
binary treatment propensity score, namely the generalised propensity score (GPS), to a
population of individuals winning the Megabucks lottery in Massachusetts in the mid-1980.
They estimate a dose-response function (DRF) for the amount of lottery prize wins on
subsequent labour earnings using the propensity score to adjust for differences in pre-
treatment characteristics. In this section, we build on the approach developed by Hirano
and Imbens (2004). As in Hirano and Imbens (2004) application, the “intensity” of
treatment depends on pre-treatment characteristics. We therefore compare individuals with
similar pre-treatment characteristics and similar GPS, i.e. predicted levels of treatment,
but different actual treatment levels.

<hs>  Implementation and estimation</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The choice of covariates depends on the behavioural factors that affect healthcare
utilisation. Education, a proxy for human capital, is related to both health knowledge and
self-management (Goldman and Smith, 2002; Cutler and Lleras-Muney, 2006). Income and
employment status are proxies for the opportunity cost of time of visiting the doctor. As
doctor consultations do not attract user charges in the UK, this is the only cost to the
individual. There is also some evidence that ethnicity affects the utilisation of primary
care in England (Goddard, 2008). Finally, we consider the number and type of health
conditions measured in each individual’s first year of observation. As there might be
interactions between these characteristics, we include interactions between types of
conditions, age and education. This categorisation of these pre-treatment variables
achieves good balance between the treatment and comparison groups. The estimation of the
dose-response function (DRF) consists of three stages, which will now be explained in
turn.

        First stage – treatment model and the balancing test

        Within each cut, we compute the GPS from Eq. (2) at the median of each cut of the
        treatment. Then, we divide each cut into blocks defined by tertiles of the GPS
        evaluated at the median, considering only the GPS distribution of individuals in
        that particular cut of medical consultations. Within each block we calculate the
        mean difference of each covariate between individuals who belong to a block of the
        cut and those who belong to other cuts. We combine all the mean differences by
        using a weighted average with weights given by the number of observations in each
        tertile of the GPS. This procedure is repeated for each of the cuts and for each
        pre-treatment characteristic. The key assumption of the first stage is that,
        conditional on the GPS, there are no statistically significant differences between
        the characteristics of individuals belonging to different treatment intervals.
        This does not necessarily imply that there are no differences in their unobserved
        characteristics.

<hs>  Supplementary analyses</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

We also undertake a range of supplementary analyses. Some of these check the robustness of
the results to the model specification; others focus on an alternative sample of
individuals who have visited the doctor at least once for preventive purposes and
implement alternative econometric techniques.

     <hss>Alternative model specifications</hss>

        We modify the main model specification in four ways. First, we modify the RE
        ordered probit model to include all the covariates used to estimate the GPS
        directly in the outcome model. Second, we modify the definition of treatment in
        the outcome models to include the number of doctor visits: i) treated as count
        variable; ii) with a set of dummies for each interval of visits; and iii) the
        prediction from the interval regression rounded to the closest integer. Third, we
        adopt the stratification method suggested by Imai and van Dyk (2004) by estimating
        the outcome model separately for each tertile of the GPS and then take the
        weighted average of the coefficients. Finally, we repeat the analysis described in
        Section 3.1 including the past frequency of physical activity in the treatment
        model. In this analysis we lose one year of data for the outcome model. Other
        specifications provide wider evidence to support the plausibility of the findings.
        We repeat the analysis for two other health behaviours, smoking and alcohol
        drinking. We consider the same years used for estimating the physical activity
        outcome models (i.e. every other year between 1996 and 2008) and focus only on
        those participating at some level in these behaviours in the first year of
        observation. We estimate treatment and outcome models for the older population
        aged 60 and over.

     <hss>Refinement of treatment</hss>

        There is a concern that reverse causation might still bias our results even after
        controlling for past physical activity, carefully selecting the timing between
        outcome and treatment, and analysing other health behaviours. We attempt to
        address this concern by selecting a sub-sample of individuals who we know have
        visited a doctor for preventive activity by undertaking at least one check-up.
        There is no other micro-level longitudinal data in the UK that asks patients the
        reason for visiting the doctor. So whilst this is only an attempt to check the
        robustness of our estimates for a sub-sample of BHPS respondents who access
        preventative health services, we acknowledge that they might have visited the
        doctor for other reasons as well. We have not found any recent aggregate figures
        for the whole of the UK reporting summary statistics on the reasons why people
        visit the doctor. However, we found that a 2013 study by the Information Service
        Division in Scotland reported that amongst the ten activities that attract most of
        the consultations in primary care practices are blood testing (500 consultations
        per 1000 population), blood pressure monitoring (350 consultations per 1000
        population) and general diagnostic tests (210 consultations per 1000 population).
        Prescription or medication review account for about 60 consultations per 1000
        population. This might suggest that most consultations are for preventive or
        monitoring purposes. Using Kaestner et al. (2014) theoretical model, for this
        group of people we can think of visits to the doctor and healthy lifestyle choices
        as two preventive activities in their health production function. A “technological
        substitution effect” might prevail if doctor contacts lower the marginal benefit
        of other health investments. For the sub-sample of people who have at least one
        check-up we re-estimate a RE ordered probit model including all the covariates in
        the treatment model.

<hs>  Main analyses</hs>
  ~~~~~~~~~~~~~

We report the results of each of the three stages for estimating the DRF, namely, the
treatment model and the balancing test, the outcome model and the DRF plot. Tables 3 and 4
report the balancing tests for each of the three cuts of the treatment, unadjusted and
adjusted for the GPS, respectively. We report a more conservative significance value at
the one percent level because of multiple comparisons over 70 variables. Table 3 shows a
high level of statistical imbalance in most of the pre-treatment covariates for each of
the cuts. Imbalance is especially high when considering socio-economic characteristics,
and the initial types and number of health conditions and visits. This indicates that BHPS
respondents who visit the doctor more or less frequently differ in their observed
characteristics. In Table 4 we show that after adjusting for the GPS we obtain a very good
balance for all of the pre-treatment characteristics. This indicates that conditional on
the GPS, BHPS respondents visiting the doctor more or less often are similar to each
other. However, we cannot assert that they have similar unobserved characteristics. As we
cannot directly interpret the magnitude of the coefficients in non-linear models, we
report marginal effects in Table 6. We compare the marginal effects from Model (III), the
static RE model with GPS, to the marginal effects from Model (IV), the dynamic RE model
with GPS. We show that the size of the effect estimated by Model (III) is double that
estimated by Model (IV) for frequency of physical activity between once a year and once a
week. The marginal effects from Model (IV) show that treatment is associated with a shift
of the distribution of physical activity to the left. An additional medical consultation
is associated with a decrease in the probability of engaging with physical activity at
least once a week by 0.5 percentage points while the probability of not doing any physical
activity at all increases by 0.4 percentage points. The changes in moderate physical
activity are smaller as, on average, an additional medical consultation is associated with
an increase in the probability to engage in physical activity between once a year and once
a month by almost 0.05 percentage points. Fig. 2 displays the linear predictions of
physical activity from the second stage non-linear regression with a range between zero
and one. The figure shows a general reduction in the level of physical activity as the
intensity of treatment increases. The slope of the DRF is steeper for more than two visits
to the doctor. This indicates a negative association between doctor visits and frequency
of physical activity that becomes stronger at higher levels of intensity.

<hs>  Supplementary analyses</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

In Table A1 we report estimates when including all the covariates from the GPS regression
directly in the outcome equation. The association between physical activity and number of
visits to the doctor remains negative and statistically significant and the size of the
coefficient is quite close to the one in Model (IV) of Table 5. Including the GPS in the
outcome model reduces the curse of dimensionality and improves efficiency because we can
just use a term (i.e. the GPS) predicted from a treatment model that includes interactions
between covariates and polynomial terms instead of individual covariates. As shown in Fig.
1 doctor visits have been predicted from a constrained model where only the bounds of the
intervals map the actual visits. There might be a concern that this prediction is driving
our results. In Table A2 we show this is not the case as the same negative association
between visits to the doctor and physical activity holds when treatment is defined as a
count variable (Model I), as a set of dummy variables (Model II) or as a prediction from
the constrained regression rounded to the closest integer (Model III). Model II shows that
the association between doctor visits and physical activity is steeper at higher intensity
levels as reported in the DRF plot. Table A3 shows that the relationship between treatment
intensity and physical activity is similar when we estimate the outcome model separately
by GPS tertiles. In Table A4 we report the results of the outcome model where GPS has been
obtained from a treatment model that includes physical activity. We show that our previous
results were not driven by the omission of past physical activity from the treatment model
as the coefficient of interest has a similar size and statistical significance. This
should alleviate concerns about reverse causality. We find a statistically significant
relationship between smoking or drinking and number of visits to the doctor. Table A5
indicates that more frequent visits to the doctor are associated with more drinking and
smoking, a similar association to the one found for physical activity. In Table A6 we
report alternative specifications to alleviate concerns of reverse causality and
unobserved confounding. All models show that there is still a negative association between
doctor visits and physical activity. We report in Table A6 the set of covariates that is
shared across all models. Model (I) is a RE ordered probit model estimated on the sample
of those who undertake at least one health check. The size of the coefficient is very
similar to the one in our preferred specification of a dynamic RE model with the GPS in
Table 5. We have also estimated Model (I) using all the specifications in Table 5 and
results are very similar (available from the authors on request). Model (II) is estimated
with a linear FE model where only time varying covariates have been included. The
coefficient on doctor visits is also very similar to our previous specifications. Models
(III–IV) report the second stage RE ordered probit coefficients of the 2SRI specification
described in Eq. (5). The negative association between number of visits to the doctor and
physical activity holds when using either spousal visits to the doctor (Model III) or area
average visits (Model IV) as instruments. The similarity of the coefficients on doctor
visits using these alternative instruments goes some way to alleviate concerns over their
limitations. The coefficient on the residuals predicted from the first stage regression is
statistically significant indicating endogeneity of visits to the doctor (Terza et al.,
2008). It can be interpreted as evidence that those who have a higher propensity to go to
the doctor have a lower propensity to engage in physical activity. As the first stage
estimates of these models are similar to those reported in Table 2, we do not report them
here, but they are available on request. Both instruments are relevant instruments as they
are positively and statistically significantly (at the one percent level) associated with
individual’s i visits to the doctor (with a coefficient of 0.02 and 0.14, respectively;
and a value of the z statistics greater than 10). In Table A7 we show that the negative
association between visits to the doctor and physical activity holds for the older
population as well. The magnitude of this relation is higher than the one found for the
sample aged between 30 and 59 years.

<h>CONCLUSIONS</h>
-----------

Healthy lifestyle choices and medical consultations can be substitute or complements in
the health production function. Although previous literature (Kaestner et al., 2014;
Schneider and Ulrich, 2008) has found evidence of substitutability, medical treatment was
measured as a dichotomous variable in these applications. In this paper we have examined
the effect of increasing treatment “intensity”, the number of doctor contacts, on
frequency of physical activity using seven waves of the BHPS. We have found evidence of a
negative association between treatment intensity and physical activity. This relationship
is stronger the higher the intensity of treatment. An additional medical consultation is
associated with a reduction in the probability of engaging in physical activity at least
once a week by 0.5 percentage points while the probability of not doing any physical
activity at all increases by 0.4 percentage points. This association is related to a shift
of the distribution of physical activity to the left towards lower frequency of
engagement. The changes in moderate physical activity are smaller as, on average, an
additional medical consultation is associated with an increase in the probability to
engage in physical activity between once a year and once a month by about 0.05 percentage
points. We have also shown that a simple regression of the number of visits to the doctor
on the frequency of physical activity suffers from selection bias and over-estimates the
relation between medical consultations and investments in health. We have attempted to
mitigate this selection bias problem with a novel application of the dose-response
function developed by Hirano and Imbens (2004) that combines the continuous treatment
approach with dynamic panel data models. Our novel methodological application has produced
three insights in the modelling of the relation between treatment intensity and healthy
lifestyle choices. Firstly, we have shown that selection bias accounts for part of the
relation between treatment intensity and healthy lifestyle choices as there is a 14%
reduction of the coefficient of treatment intensity when the generalised propensity score
(GPS) is included in the regression. Secondly, the dose-response function with the GPS
could lead to efficiency gains as it allows confounders to enter flexibly in the outcome
model via the GPS that can then be stratified and modelled with higher polynomial orders.
Our results suggest that accounting for non-linearities in the characteristics determining
treatment selection is important as the second-order polynomial of the GPS is
statistically significant in the outcome regression. Finally, combining dynamic models and
a dose-response function with the GPS has the advantage to flexibly account for treatment
selection, unobserved heterogeneity and the dynamic nature of healthy lifestyle choices.
We have found the size of selection bias is lower as there is an almost 42% reduction in
the coefficient of treatment intensity when we estimate the dose-response function in a
dynamic random effects model (i.e. including both the GPS and the lagged values of the
outcome variable). One limitation of our paper is that the measure of frequency of
physical activity is only limited to playing sports, swimming or walking. Whilst this is
the only type of physical activity that is consistently measured across the BHPS sample,
we have shown evidence of a negative association between treatment intensity and other
healthy lifestyle behaviours such as reducing cigarettes and alcohol consumption. A second
limitation which we share with the study by Hirano and Imbens (2004) is the lack of
exogenous variation in treatment. The application by Hirano and Imbens (2004) focused on a
cross-section of lottery winnings which although exogenous belong to a particular selected
sample of players. Although we combine dynamic panel data models with the GPS, we are
cautious in asserting we are estimating a causal effect. We have attempted to mitigate
this limitation by using 2SRI models with spousal and area-average visits to the doctor as
instruments. Both instruments have advantages and disadvantages relating to the amount of
variation and the potential for direct pathways to physical activity. Under the assumption
of time-invariant unobserved heterogeneity we have estimated a FE model. Although our
results are robust to both specifications, we note that time-varying unobserved
heterogeneity and omitted variable bias might still be possible. A third limitation is
that, in following Bia and Mattei (2008), Hirano and Imbens (2004) and Imbens (2000), we
do not correct the standard errors for the inclusion of the GPS in the outcome model. A
final limitation is that we cannot determine what elements of the treatment generate an
inverse relationship with healthy lifestyle choices, as the dataset contains no
information on the cause and content of doctor consultations. The non-linear association
between doctor visits and frequency of physical activity might be concerning if an
unobserved (to us as researchers) health problem has induced patients to initiate a doctor
visit. This would generate a non-linear and reverse causal association between doctor
visits and frequency of physical activity. There is no longitudinal survey data in the UK
that asks respondents the reason for visiting the doctor. Instead, we have shown that our
results are robust to restricting our sample to individuals who have had at least one
preventative health check-up. Official statistics suggest that the majority of doctor
consultations are for preventive purposes. These two pieces of information point to the
direction of a substitution between two preventive activities in the health production
function. However, we highlight that data do not allow us to ascertain the reason for
visiting the doctor and therefore we cannot give a causal interpretation to the estimates
produced in this study.


<h>REFERENCES</h>
----------

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<ART>Major correlates of male height: A study of 105 countries
=========================================================

Authors: P. Grasgruber, M. Sebera, E. Hrazdíra, J. Cacek, T. Kalina
DOI: 10.1016/j.ehb.2016.01.005
Year: 2016  |  Pages: 172-195
ASJC codes: 2001
Keywords: Asia, Europe, Genetics, Male height, Nutrition

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

The purpose of this study is to explore the main correlates of male height in 105 countries in Europe & overseas, Asia, North Africa and Oceania. Actual data on male height are compared with the average consumption of 28 protein sources (FAOSTAT, 1993-2009) and seven socioeconomic indicators (according to the World Bank, the CIA World Factbook and the United Nations). This comparison identified three fundamental types of diets based on rice, wheat and milk, respectively. The consumption of rice dominates in tropical Asia, where it is accompanied by a very low total protein and energy intake, and one of the shortest statures in the world (∼162-168 cm). Wheat prevails in Muslim countries in North Africa and the Near East, which is where we also observe the highest plant protein consumption in the world and moderately tall statures that do not exceed 174 cm. In taller nations, the intake of protein and energy no longer fundamentally rises, but the consumption of plant proteins markedly decreases at the expense of animal proteins, especially those from dairy. Their highest consumption rates can be found in Northern and Central Europe, with the global peak of male height in the Netherlands (184 cm). In general, when only the complete data from 72 countries were considered, the consumption of protein from the five most correlated foods (r = 0.85) and the human development index (r = 0.84) are most strongly associated with tall statures. A notable finding is the low consumption of the most correlated proteins in Muslim oil superpowers and highly developed countries of East Asia, which could explain their lagging behind Europe in terms of physical stature.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

In our previous study (Grasgruber et al., 2014), we identified nutrition and genetics as
the strongest correlates of height among contemporary young men from 42 European and three
overseas countries (Australia, New Zealand and the USA). Out of all the socioeconomic
factors that were examined, only children's mortality approached the significance of
nutrition and genetics, which points to the importance of a disease-free environment.
Improved nutrition and better healthcare are direct consequences of improving living
standards that accompanied the process of the industrial revolution (Hatton, 2013). In the
present study, we aim to extend this research to North Africa, Asia and Oceania. These
regions include mostly developing countries, but Muslim oil superpowers (Bahrain, Brunei,
Kuwait, Oman, Qatar, Saudi Arabia and the United Arab Emirates/UAE) and some developed
countries of East Asia (Japan, Singapore, South Korea, Taiwan) currently belong to the
wealthiest in the world, with the gross domestic product (GDP) per capita higher than
30,000 USD (World Bank, 2013), not to mention the semi-independent territory of Hong Kong.
Interestingly, male height in some of these regions (Arab countries of North Africa and
the Near East) was once similar or even higher than in Europe, but after the 1880s it
started to lag behind considerably (Stegl and Baten, 2009). On the other hand, wealthy
nations of East Asia are still known for their surprisingly small stature, despite very
high values of the GDP per capita (Baten and Blum, 2014). Therefore, it would be important
to identify the main factors that currently distinguish these regions from Europe. As we
did similarly in our previous study, we plan to explore the correlation of factors such as
nutrition, healthcare and national wealth with the height of contemporary young men.
Genetic factors (frequencies of Y haplogroups) are included as well, but in a
supplementary function, because no Y haplogroup is shared in appreciable frequencies
across the whole area of Europe, North Africa, Asia and Oceania.

<hs>  Collection of anthropometric data</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The selected regions of North Africa, Asia and Oceania encompass 63 countries (including
three semi-independent territories–American Samoa, French Polynesia, Hong Kong), for which
data on body height were researched. In Oceania, only more populous countries with a
population size exceeding 50,000 inhabitants were considered, because statistics were not
available for small island nations. Preferably, we searched for anthropometric data on
young, mature men aged 18–30 years (but ideally 20–25 years) from the time after the year
2000. Only surveys that incorporated at least 50 individuals were used, but whenever
possible, nationwide surveys with more than 200 individuals were preferred. The only
samples with fewer than 100 individuals were from Guam (n = 59) and Algeria (n = 55)1. By
far the most representative data (regular measurements of recruits) were available from
Israel, but paradoxically, they were the most problematic due to the inclusion of young
immigrants, who were not born and raised in Israel2. The majority of surveys included in
our study are nationwide health surveys incorporating all social groups. Some other
surveys had certain limitations. Six of them (from Bhutan, Laos, Libya, Oman, the Maldives
and Syria) incorporate an urban population from a single city. The sample from Libya
consists of patients visiting a hospital in Derna. Three surveys (from Saudi Arabia, the
United Arab Emirates and the Federative States of Micronesia) come from a specific region
of the country. The sample from North Korea includes refugees. In the case of Afghanistan,
Kyrgyzstan, Pakistan, Tajikistan and Turkmenistan, the male height was estimated, based on
highly representative studies of local women. The height in Kazakhstan (175.6 cm) was
computed from the data of Facchini et al. (2007). (See Appendix: Methods for a more
detailed discussion.) Due to the scarcity of information from some countries, certain
compromises needed to be made. This especially concerns the STEPS surveys (Noncommunicable
Disease Risk Factor Surveys) performed by the World Health Organization (WHO), which
rarely include people younger than 25 years and routinely start with the age category of
25–34 years. Nevertheless, it is unlikely that the inclusion of older subjects would
markedly distort our results, because the pace of the secular trend in the majority of the
examined countries is very slow or almost non-existent. Besides that, some means of male
height from our previous study were updated. This update relates to Bosnia and
Herzegovina, Bulgaria, the Czech Republic, Georgia, Moldova and Ukraine (see Appendix:
Methods and Appendix Table 1). Recent anthropometric data were even obtained from Armenia,
but they did not seem to be sufficiently representative. Nevertheless, they indirectly
supported the accuracy of our male estimate based on DHS 2005 (171.9 cm)3. Altogether,
information on body height was collected from 61 out of 63 targeted countries (Table 1).
Only data from Macau and New Caledonia were missing4. Our list also includes the Maori,
but considering that they make up a minority in New Zealand, this sample was not useable.

<hs>  Collection of nutritional and sociodemographic data</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The information about the average daily protein consumption (in grams) was computed from
FAOSTAT.org5. The statistics on the gross domestic product (GDP) per capita (by purchasing
power parity/PPP, in current international USD), health expenditure per capita (by PPP, in
constant 2005 international USD), urbanization (% of urban population), children's
mortality under 5 years (per 1000 live births) and total fertility rate (births per woman)
were taken from the World Bank6, and the Gini index of social inequality from the CIA
World Factbook7. In addition, we included the human development index (HDI) that is
regularly calculated by the United Nations8. Since 2010, the HDI has been computed from
the statistics of life expectancy, mean and expected years of schooling, and the GDP per
capita by PPP. To obtain the most precise results, we extended the period, for which the
average values of nutritional and sociodemographic data were calculated (from 2000 up to
1993), but this required the elimination of Montenegro from the European sample, because
many key data from Montenegro would be missing. A further historical extension (before
1993) was not possible, because many statistics from the disintegrated countries of the
former Communist bloc have been available only since 1993. The information on the GDP and
health expenditure has been complete since 1995. The average daily protein consumption,
children's mortality, total fertility and urbanization were therefore computed for the
period 1993–2009 and the GDP and health expenditure for 1995–2009. The data of the Gini
index were computed as averages of all the available values from 1990 to 2013. Considering
that the historical HDI data were often incomplete, only the HDI values from 2011 were
used. This limitation should not pose a problem, because HDI values largely summarize the
societal development in the near past. Furthermore, the use of the HDI from 2011 enabled a
mutual comparison with the newly introduced ‘inequality-adjusted HDI’ (IHDI), which takes
the demographic variance in the HDI indicators into account. Altogether, information was
collected on male height from 106 countries (including Montenegro), on urbanization from
105 countries, on total fertility from 102 countries, on children's mortality from 101
countries, on the HDI from 100 countries, on health expenditure from 97 countries, on the
GDP from 96 countries, on protein consumption from 93 countries, but on the Gini index
only from 80 countries. All the data were available for 72 countries.

<hs>  Collection of genetic data</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~

For the genetic comparison, we use frequencies of Y haplogroups (male lineages)9. Y
haplogroups usually show a more refined geographical pattern than mtDNA haplogroups
(female lineages), because males rarely leave their ‘clan’ (Rosser et al., 2000). This is
also evident from the fact that the distribution of Y haplogroups correlates with certain
language groups10. Therefore, it is more likely that Y haplogroups will be associated with
the prevalence of certain physical traits, because they mostly evolved within separate
patrilocal communities. As shown by the results of our previous study, typical European Y
haplogroups correlate quite strongly both with male height and with the prevalence of
lactose tolerance. The relationship between the combined frequency of Y haplogroups I-M170
& R1b-U106 and male height in 34 countries reached r = 0.75 (p < 0.001). It is true that a
recent study by Robinson et al. (2015) attributed only 24% of the height differences among
14 European countries to genetic differences, but this percentage may be underestimated,
because this study apparently used very low height values of the whole male population and
it did not include any samples from the Western Balkans. In the present study, two major
regions with a relatively high frequency of particular Y haplogroups are examined. In
North Africa and the Near East (including Turkey and the Caucasian republics), six major Y
haplogroups were selected: E1b1b1a1-M78 (E1b-M78), E1b1b1b1a-M81 (E1b-M81), G-M201,
J1-M267, J2-M172 and R1a-M420. Data on the frequency of these Y haplogroups were available
from 21 countries (Appendix Table 2a). Only representative information on Bahrain and
Israel was missing. In South, Southeast & East Asia and Oceania, four Y haplogroups were
selected: O1-MSY2.2, O2-P31, O2a-PK4 and O3-M122 (Appendix Table 2b). Data from this
region are still quite scarce and often confined to specific areas or tribal groups; hence
information from 8 out of 35 targeted countries was missing. Data on the phenotypic
prevalence of lactose tolerance are taken from three main sources: the Global Lactase
Persistence Association Database, Ingram et al. (2009) and Flatz and Rotthauwe (1977).
Only studies incorporating ≥50 individuals were used, which limited the number of
countries to 20 (see Appendix Table 3). When combined with the countries examined in our
previous study, the prevalence of lactose tolerance was available for 47 countries.

<hs>  Statistical analyses</hs>
  ~~~~~~~~~~~~~~~~~~~~

Statistical analyses were conducted by the software Statistica 12. A standard comparison
via Pearson linear correlations was performed between male height and all the data that
were available (Tables 2 and 3a–3b). Because complete information was not available for
all the countries, the number of countries differed from variable to variable. To make the
results comparable, we undertook an additional, separate analysis with only 72 countries,
for which all the information was available (Table 3b and Appendix Table 4). These 72
countries were also subsequently used in a multiple regression. The drawback of this
limited sample was the complete absence of Oceania and many Muslim countries. Therefore,
an additional regression analysis with 83 countries (without the Gini index) was
performed, but as we will show below, there were only small differences in the results.
More sophisticated statistical procedures such as the use of instrumental variables were
also considered, but we failed to find a variable that would be useful for such models.

<hs>  Distribution of male height</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~

The data collected from 61 countries/regions are summarized in Table 1 and the
geographical comparison of all 106 countries is displayed in Fig. 1. The range of values
is very wide, from 161.6 cm in Timor-Leste up to 183.8 cm in the Netherlands (22.2 cm).
Very tall statures above 180 cm are typical only of Europe, especially the areas with the
highest frequency of Y-haplogroups I-M170, R1b-U106 and R1a-M42011, and the highest
quality of nutrition. The lowest values (below 165 cm) can be found in Yemen and Southeast
Asia (Timor-Leste, Cambodia, Bangladesh etc.). Highly developed countries in East Asia
(Japan, Singapore, South Korea, Taiwan), China and Muslim countries in North Africa and
the Near East are positioned roughly in the middle, with heights fluctuating around 170
cm. The Lebanese (175.5 cm) and most likely even the people of Kazakhstan (ca. 175.6 cm)
are by far the tallest in Asia. Somewhat surprisingly, the average height in highly-
developed Israel (174.5 cm) is shorter than that in Lebanon, and this is true even after
the exclusion of 19-year old recruits, who were sons of recent immigrants and were not
born in Israel. The small sample of Algerians (174.6 cm) is the tallest in North Africa.
However, their stature is still only comparable to that of the shortest nations of Europe.
Remarkably, it is Polynesians, who reach the highest values among the 61 new samples, more
specifically the inhabitants of French Polynesia (178.6 cm)12, Tonga (176.7 cm)13 and
American Samoa (175.9 cm)14. Marked geographical changes in male stature are hidden in the
national averages of the largest countries—China and India. Zhang and Wang (2011) recently
analysed data from the nationwide health survey in China (2005) and found that the height
in 30 Chinese provinces (except Tibet) ranged from 165.6 cm for men in rural areas of the
Guizhou province to 175.4 cm for men in urban areas of the Liaoning province. If the data
from urban and rural areas from this study are pooled, the tallest statures can generally
be found in northeastern provinces around the Yellow Sea such as Beijing (174.5 cm),
Liaoning and Shandong (both 174.2 cm), while small statures are typical of southern
regions, particularly the provinces of Chongqing (167.1 cm) and Guizhou (166.5 cm) (see
Appendix Fig. 1). The geographical changes of male stature in India are comparably large.
According to the most recent Indian nationwide survey (NFHS 2005–2006; Mamidi et al.,
2011), the highest male averages in the age category 20–29 years were documented in
northwestern states—Punjab (168.4 cm), Haryana (168.1 cm) and Jammu and Kashmir (168.0
cm). The shortest statures are typical of northeastern states—Meghalaya (157.5 cm), Sikkim
(160.0 cm) and Arunachal Pradesh (161.0 cm) (Appendix Fig. 2)15.

<hs>  GDP per capita</hs>
  ~~~~~~~~~~~~~~

The correlations of male height with the GDP per capita and other socioeconomic indicators
are summarized in Table 2. Although the growing GDP per capita has been the fundamental
trigger of the positive height trend during the last century, it fails to be a good
correlate of male height in 96 countries (r = 0.30; p = 0.003) (Fig. 2). This is primarily
due to two reasons: First, as we showed in our previous study, the relationship between
height and GDP in Europe was distorted by the historical division into the “Western” and
“Communist” blocs. Communist countries lagged behind in terms of economic development, but
historically, the wealthiest of them were characterized by a diet associated with tall
statures, which is based on milk products, pork and fish. In contrast, the dietary customs
in some “Western” countries such as Portugal, Spain, Italy and Greece were different and
only began to change in a similar way during the most recent decades. Second, the high GDP
per capita in Muslim oil superpowers, as well as in the wealthy countries of East Asia, is
not accompanied by the same type of nutrition or public expenses on healthcare that we
find in the tallest nations. This will be the subject of the upcoming paragraphs in this
section.

<hs>  Health expenditure per capita</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Health expenditure turns out to be a much better correlate of male height than the GDP (r
= 0.60; p < 0.001 in 97 countries) (Appendix Fig. 3). This is mainly due to the fact that
the public health expenses in Muslim oil superpowers are much lower than their GDP would
predict and are more in line with the unimpressive height of the local young men. Such a
striking discrepancy points to a strongly uneven redistribution of yields from the oil
industry.

<hs>  Children's mortality under five years</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The most significant socioeconomic factor out of the six that we examined in our previous
study is again children's mortality (r = −0.73; p < 0.001 in 101 countries) (Fig. 3). This
result remains valid even in the sample of 72 countries, for which all the data were
available (r = −0.78; p < 0.001) (Table 2). The range of values is enormous, from ∼4 in
Finland, Iceland, Singapore and Sweden up to 132 deaths/1000 live births in Afghanistan.
Interestingly, the low children's mortality rate in tropical Asia, East Asia and Muslim
oil superpowers has no influence on the stature of local males.

<hs>  Total fertility</hs>
  ~~~~~~~~~~~~~~~

Total fertility (r = −0.64; p < 0.001 in 102 countries) follows children's mortality as
the second strongest socioeconomic correlate (Fig. 4). Although total fertility plays only
a marginal role in Europe (r = −0.26; p = 0.09), where fertility rates are almost
unanimously very low, it reaches statistical significance in the global context, because
the fertility level in developing countries is still high. It is logical to assume that
the lower the number of children per family, the higher the financial expenditures per
child would be, and hence the living conditions of the children would improve. Again, it
is noteworthy that this assumption does not apply so well to tropical and East Asia, where
the birth rates are similarly low or even lower than those in Europe, but the difference
in body height is still 10–20 cm. On the other hand, the birth rates in Muslim oil
superpowers are unusually high for the standards seen in developed countries, reaching
almost 4.0 in Oman and Saudi Arabia, and exceeding other Arab countries with a
substantially lower GDP. This could serve as further indirect evidence that their high GDP
does not translate into adequately high living standards for most of the population and/or
the degree of societal development.

<hs>  Urbanization (% of urban population)</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The correlation between urbanization and height is almost as strong as in the case of
total fertility (r = 0.58; p < 0.001 in 105 countries) (Appendix Fig. 4). In general, the
highest rates of urbanization are typical of Europe, Muslim countries and the highly
developed countries of East Asia, but they have a much weaker correlation with height in
the latter two.

<hs>  Gini index</hs>
  ~~~~~~~~~~

The Gini index, as the indicator of social inequality, does not show any statistical
relationship with height in non-European countries (r = −0.04; p = 0.80), because the
levels of social inequality are universally very high. This factor reaches significance
only in Europe (r = −0.36; p = 0.017) and in the total sample of 80 countries (r = −0.51;
p < 0.001) (Appendix Fig. 5). The Gini index tends to decrease with a growing GDP per
capita (r = −0.29; p = 0.010), and countries in tropical Asia and Central Asia are the
most affected by the combination of extreme poverty and deep social inequality (Appendix
Fig. 6). It is symptomatic that data on the Gini index are not available from wealthy oil
superpowers such as Saudi Arabia, Kuwait or Bahrain.

<hs>  Human development index (HDI)</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

This comparison proved to be a very interesting addition to our analysis, because it shows
one of the highest correlations with male height (r = 0.80; p < 0.001 in 100 countries)
(Fig. 5). Height and the HDI seem to be largely interchangeable as indicators of human
well-being. They are both related to the GDP per capita. High life expectancy is a factor
that reflects the quality of healthcare and nutrition. Furthermore, better education of
women translates into a lower fertility rate (Basu, 2002). The relationship between male
height and the IHDI (inequality-adjusted HDI) (r = 0.87; p < 0.001 in 72 countries)
(Appendix Fig. 7) is even stronger than in the case of the HDI, but if we consider only
this sample of 72 countries, for which both these indicators are available, we find no
difference in r-values. The difference between the HDI and the IHDI (a benchmark for
social equality) is a good correlate of male height as well (r = −0.64; p < 0.001)
(Appendix Fig. 8).

<hs>  Nutrition</hs>
  ~~~~~~~~~

Because our present study incorporated FAOSTAT data from a longer period of time
(1993–2009), it is not surprising that the correlation coefficients in our European sample
of 44 countries are often higher (Table 3a). Three additional protein sources (meat total,
pelagic marine fish, eggs) reach significance and the position of milk products as key
stimulators of physical growth is further strengthened (r = 0.50; p < 0.001). As already
mentioned in our previous study, these findings have a very solid rationale, because milk
products, red meat, eggs and some species of fish have the highest protein quality out of
all common foods. The situation in 49 non-European countries is very different. The main
correlate of height is not protein quality, but total protein consumption (protein
quantity) (r = 0.71; p < 0.001). Fig. 6 shows that total protein consumption in tropical
Asia and some other countries such as Tajikistan, Iraq, Afghanistan or the Solomon Islands
is extremely low. The main socioeconomic factor boosting total protein intake in 72
countries is the HDI (r = 0.81; p < 0.001), followed by urbanization (r = 0.78; p < 0.001)
and the GDP per capita (r = 0.76; p < 0.001). When these variables were assessed
individually and the number of countries examined was thus greater, the association
between total protein and GDP per capita in 85 countries decreased (r = 0.65; p < 0.001),
because Muslim oil superpowers such as the UAE, Kuwait and Brunei emerged as striking
outliers that consume less protein than their high GDP would predict (Appendix Fig. 10a).
With the increasing consumption of total protein, there are large differences in height at
the same consumption level (10+ cm), which points to the importance of protein quality.
Other highly significant nutritional correlates of male stature in 49 non-European
countries are total energy intake (r = 0.70; p < 0.001) (Appendix Fig. 9), rice protein (r
= −0.65; p < 0.001) and wheat protein (r = 0.62; p < 0.001) (Fig. 7). Rice is the main
source of protein in tropical Asia (particularly in Laos, Cambodia and Bangladesh; >30
g/day), which is where we encounter extremely small height means of ∼162–168 cm. The level
of rice protein consumption is quite high even in Japan, China and both North and South
Korea (>10 g/day). Remarkably, wheat protein correlates with male stature negatively in
Europe (r = −0.68; p < 0.001), but positively outside Europe. When rice consumption
decreases, wheat consumption increases (Appendix Fig. 11a) and so do the values of male
stature (Fig. 7 and Appendix Fig. 11b). The intake of total energy and total protein
increases as well. The positive height tendencies tied to the increasing consumption rates
of wheat reach a peak of ∼174 cm in Muslim countries of North Africa and the Near East
(Turkey, Tunisia, Azerbaijan). The consumption of vegetables and legumes in this region is
very high as well and the proportion of animal proteins is moderate. As a result, some of
these countries (Turkey, Egypt, Morocco) consume the largest amounts of plant protein in
the world (Appendix Fig. 12). In taller nations, the intake of total protein and total
energy is no longer rising fundamentally, but plant proteins are substituted by animal
proteins (particularly dairy proteins) (Appendix Fig. 13). Consequently, the relationship
between most plant proteins and male height is curvilinear (Appendix Fig. 12), similar to
that between GDP per capita and plant protein (Appendix Fig. 10b). The animal protein
intake in 72 countries rises very strongly with the HDI (r = 0.89; p < 0.001) and GDP per
capita (r = 0.87; p < 0.001). Muslim oil superpowers consume much less animal protein than
their high GDP per capita predicts, which again decreases the r-values, when 85 countries
are considered (r = 0.67; p < 0.001) (Appendix Fig. 10c). The intake of protein from milk
products (dairy proteins) emerges as the most significant nutritional correlate of stature
not only in Europe, but in all 93 countries examined in this study (r = 0.79; p < 0.001)
(Table 3b; Appendix Fig. 14), followed by total protein (r = 0.74; p < 0.001) and animal
protein (r = 0.73; p < 0.001). The most negative nutritional correlate in the total sample
is again rice (r = −0.74; p < 0.001). Dairy proteins are most frequently consumed in the
Netherlands, Sweden and Finland (almost 30 g/day), while in countries from the eastern
half of Asia such as Cambodia, Laos or North Korea, their intake is virtually zero.
Remarkably, this low intake of milk products is in accordance with the low prevalence of
lactose tolerance in Southeast and East Asia (Appendix Fig. 15a) and the widespread
undernutrition in this region. These facts confirm the fundamental evolutionary
significance of lactose tolerance in a world, where the scarcity of valuable nutrients is
an everyday reality16. Similarly to our previous study, we tried to find ratios or
combinations of protein intake that would further improve the predictive power. The ratios
between animal proteins and plant/cereal protein were not useful in this regard, but
combinations of proteins were. Pork protein has the biggest additive effect, when combined
with dairy proteins (r = 0.82; p < 0.001), followed by protein from eggs (r = 0.81) and
potatoes (r = 0.81). The correlation reaches r = 0.84, when potatoes are added to dairy
and pork. The highest r-value (r = 0.85) was achieved via the combination of proteins from
dairy, pork, beef, eggs and potatoes (‘highly correlated proteins’). The strength of this
relationship is visually impressive (Fig. 8). ‘Highly correlated proteins’ are also the
strongest correlate of male height (r = 0.85), when all the nutritional and socioeconomic
variables from 72 countries are considered (Table 3b). Interestingly, in this sample of 72
countries, ‘highly correlated proteins’ are strongly associated with the HDI (r = 0.82)
and GDP per capita (r = 0.77; p < 0.001), but the addition of wealthy Arab countries again
decreases the relationship with the GDP per capita very noticeably (r = 0.49; p < 0.001)
(Appendix Fig. 10d). While Europeans often consume more of these proteins than their GDP
per capita would predict, wealthy, short-statured Muslims and East Asians consume less.
‘Highly correlated proteins’ are also strongly associated with lactose tolerance (r =
0.80; p < 0.001), although in this case, the number of countries was limited to only 44.
The relationships of nutrition with various socioeconomic factors and lactose tolerance
are presented in Appendix Tables 5a–5e. These results confirm that red meat and eggs are
the most height-related components of the human diet after milk, which primarily stems
from the complete amino acid spectrum of their proteins (Appendix Table 6). Our
calculations show that at least in Europe and overseas, the correlation of eight main food
items with height accords better with their amino acid scores based on the older FAO
standard 1985 than the newer FAO standard 2007 (see Appendix Tables 7a and 7b). More
concretely, the new FAO standard 2007 produces relatively higher amino acid scores for
beef and fish, and a relatively lower amino acid score for pork. This is mainly due to the
marked decrease of tryptophan content in the new standard17. The role of pork in our
analysis is weakened because of its absence from the diet of Muslim countries (Appendix
Fig. 17), but its statistical relationship with stature is still stronger than that of
beef and fish, when all 93 countries are considered. Therefore, we think that in the light
of the admitted imperfection of the current amino acid scores18, the results of our
ecological study should be taken into account seriously. On the other hand, the
significance of potatoes, even as an independent item (r = 0.68; p < 0.001), is unexpected
because of the poor quality of potato proteins, their low consumption rate and a very low
‘nutrient density’19. Therefore, we cannot exclude that the correlation between potatoes
and height is only spurious. Nevertheless, it is visually quite persuasive (Appendix Fig.
18) and the rationale behind this finding deserves further discussion20. In contrast with
Europe, fish consumption does not contribute positively to male stature in the total
sample of 93 countries (r = −0.15; p = 0.16) and freshwater fish even correlate slightly
negatively (r = −0.21; p = 0.047). This result is largely deceptive, because fish
consumption shows some positive relationship with male height, when the examined countries
are divided according to regions (Appendix Fig. 19). In Southeast Asia, Japan and many
countries in Oceania, fish remain the main source of animal protein. Other protein items
with a high height correlation are not consumed in large quantities. Furthermore, there
are big differences in protein quality among various species of fish. When the food items
with the most negative r-values (rice and legumes) are combined, a small additive effect
is observed, when compared with rice alone (r = −0.75; p < 0.001) (Appendix Fig. 20). The
proportion of energy intake from protein (assuming 4.1 kcal per 1 gram of protein) clearly
highlights the low ‘nutrient density’ of the diet in tropical Asia (Appendix Fig. 21).

<hs>  Current nutritional trends in Asia, North Africa and Oceania</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The evidence presented in the previous paragraphs can persuasively explain, why many
wealthy Asian countries have a smaller physical stature than European countries. A high
GDP, high rates of urbanization, low children's mortality rate, high indices of human
development and mostly above-average health expenditure and below-average fertility rates
are not sufficient to compensate for the persisting low intake of the proteins that are
most strongly associated with tall stature in the present study. In fact, the intake of
‘highly correlated proteins’ in Kuwait, the UAE, Japan and South Korea is on the level of
the poorest European countries such as Georgia and Moldova (Fig. 8). Furthermore, the
level of social inequality is apparently higher than it is in the European nations with
the tallest people. We can also justly suspect that the data on the Gini index from rich
oil superpowers are not published for a good reason, because the disparity in the
distribution of national wealth may have no parallel to the rest of the world. Therefore,
the consumption of high-quality animal proteins could theoretically predict future
development. A particularly fast increase in stature can be expected in Kazakhstan,
Myanmar and Vietnam, where the annual animal protein intake during the decade 2001–2011
rose by >15 g (Fig. 9). A fast upward rate (>8 g/decade) can even be observed in China,
Morocco, Turkmenistan and South Korea. In contrast, the amount of animal proteins consumed
has more or less declined in Afghanistan, Japan, Lebanon, Mongolia, Palestine, the Solomon
Islands and the UAE. An extremely low level of consumption (∼10 g/day) combined with a
stagnating or only negligibly growing trend line, is typical of Bangladesh, India, Iraq,
Laos, Nepal, North Korea, Tajikistan and Yemen.

<hs>  Genetics: North Africa and the Near East</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As already noted in the introduction, testing the relationship between height and genetic
markers plays only a supplementary role in the present analysis, because the distribution
of certain Y haplogroups is geographically limited. In 21 countries of the targeted
regions of North Africa and the Near East, the only haplogroup that shows a significant,
negative relationship with male height is J1-M267 (r = −0.68; p < 0.001) (Fig. 10a).
J1-M267 is a signature of human populations that expanded from the Zagros Mountains during
the Holocene and its dominant sublineage J1a2b-P58 (formerly J1e) has been connected with
the spread of pastoral nomadism in the Arabian Peninsula (Chiaroni et al., 2010). Today,
the frequencies of J1-M267 peak in Yemen (73%), followed by other countries of the Arabian
Peninsula (∼35–60%) and speakers of Northeast Caucasian languages (>50%). The role of
J1-M267 remains robust (p < 0.01) even after controlling for protein consumption and all
the socioeconomic variables, except total fertility (p = 0.14). Among the four remaining
haplogroups, G-M201 approaches significance as a correlate of taller statures (r = 0.41; p
= 0.07) (Fig. 10b). This lineage reaches the highest frequencies in Georgia (39%) and is
much rarer elsewhere (18% in Azerbaijan, 12% in Iran, 11% in Turkey). The positive effect
of G-M201 becomes statistically significant, when North Africa is excluded (r = 0.55; p =
0.028). The Anatolian Neolithic lineage J2-M172 (r = 0.21; p = 0.36), as well as the East
African haplogroup E1b-M78 (r = 0.21; p = 0.36) and the Northwest African (Berber)
haplogroup E1b-M81 (r = 0.20; p = 0.38) have a non-significant, but still somewhat
positive association with height. Interestingly, the combination of G-M201 and E-M78
correlates significantly positively with height (r = 0.48; p = 0.027) and three presumably
‘agricultural’ haplogroups G-M201, E1b-M78 and J2-M172 approach statistical significance
(r = 0.40; p = 0.07) (Fig. 10b)21. When E-M81 is added to these three haplogroups, the
r-value markedly rises to r = 0.57 (p = 0.008). The addition of the Indo-Iranian genetic
signature R1a-M420 further increases the correlation coefficient to r = 0.62 (p = 0.003)
(Fig. 10c), although R1a-M420 by itself shows no relationship with height (r = 0.11; p =
0.63), which must primarily be ascribed to its low frequencies across the examined
regions. The significance (p < 0.05) of these five combined Y haplogroups persists after
controlling for all the socioeconomic variables and nutrition, but again, total fertility
decreases it the most relatively (p = 0.04). These results indicate that J1-M267 is the
major genetic correlate of short stature in the Near East and North Africa, whereas
G-M201, E1b-M78, E1b-M81, J2-M172 and R1a-M420 appear to have a positive effect, although
it manifests significantly only when the frequencies of these five haplogroups are
combined. According to these data, the greatest potential for height could be expected in
Moroccans, Tunisians and Georgians, and the lowest in Yemenites. The only other factor
that markedly decreases the significance of these results is total fertility.

<hs>  The independent evolution of lactose tolerance in Europe and Arabia</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The polarity between the ‘pastoral’ haplogroup J1-M267 and the ‘agricultural’ haplogroups
G-M201, J2-M172 and E1b-M78 does not seem to be limited to body height. J1-M267 namely
lies at the epicentre of another global peak of lactose tolerance, as evidenced by
relatively high prevalence values from Jordan (51%), Kuwait (53%) and Saudi Arabia (56%).
Indeed, lactose tolerance has a high positive correlation with J1-M267 (r = 0.87; p =
0.023) (Appendix Fig. 22a), but a high negative correlation with E1b-M78, G-M201 and
J2-M172 (r = −0.89; p = 0.019) (Appendix Fig. 22b). Although these results are based on
only six countries, they are definitely intriguing, because the evolution of lactose
tolerance within pastoral communities of J1-M267 makes good sense. In addition, in our
previous paper we found that the combined frequencies of E1b-M78, G-M201 and J-P209
correlated strongly negatively with lactose tolerance even in Europe (r = −0.73; p <
0.001). This finding could potentially question the calculations of Itan et al. (2009),
who propose that the genes of lactose tolerance in Europe were inherited from early
Central European farmers. At the same time, it is important to note that the alleles
determining lactose tolerance in Europe (−13910 * T) and in Arabia (−13915 * G) are
different, which shows that this genetic trait developed independently (Ingram et al.,
2009). The data from our previous study show that the spread of lactose tolerance in
Europe is most closely tied to Y haplogroups I-M170 & R1b-U106 and the area of the North
German plain22. The first appearance of this genetic trait can be dated to the Late
Neolithic/Early Bronze Age (fourth to third millenium BC), which is already supported by
paleogenetic data (Allentoft et al., 2015; Mathieson et al., 2015a). This period is
characterized by the expansion of the Corded Ware culture in Northern and Central Europe,
and a sudden dramatic increase in male stature of ∼7 cm. However, the subsequent
dissemination of lactose tolerance in Western Europe and the British Isles must be
connected with some other cultural circles, most probably the Bell Beaker culture (in the
late third millenium BC) and Y haplogroup R1b-S11623. This assumption can already be
supported by the first concrete paleogenetic evidence (Cassidy et al., 2015).
Interestingly, other paleogenetic studies using autosomal DNA (Allentoft et al., 2015;
Haak et al., 2015; Mathieson et al., 2015a, 2015b) suggest a more complex scenario. The
populations carrying I-M170 & R1b-U106 may have originally acquired lactose tolerance from
the pastoral Yamnaya people, who migrated to Central Europe from the Pontic/Caspian steppe
around 3000 BC and formed the basis of the Corded Ware culture. This assumption is based
on the strikingly high frequency of lactose tolerance in the Yamnaya culture and even
other related steppe cultures of Central Asia (Afanasievo, Mezhovskaya, Karasuk; fourth to
second millenium BC) (Allentoft et al., 2015), of which at least the latter two could be
connected with Indo-Iranian speakers. Indeed, the allele that is responsible for the
relatively high lactose tolerance in Pakistan (47%) and India (38%) is identical to −13910
* T from Europe (Ingram et al., 2009) (Appendix Fig. 15b). Furthermore, a positive
geographical connection appears to exist between lactose tolerance in Central Asia/India
and Y haplogroup R1a-Z93—a specific Indo-Iranian subbranch of R1a-M420 identified by
Underhill et al. (2015) (Appendix Fig. 16). An eastern migration to Central Europe during
the Late Neolithic/Bronze Age is also reflected by the very high (50%) frequencies of
R1a-M420 in the available samples of Corded Ware males (Mathieson et al., 2015b), but as
we emphasized in our previous article, R1a-M420 correlates slightly negatively with
lactose tolerance in today's Europe (r = −0.10; p = 0.62) (see Appendix Fig. 15a). Only
the combined frequency of two minor subbranches typical of Germanic speaking nations
(R1a-Z284 and R1a-M417*) shows a certain positive relationship (r = 0.45; p = 0.045 in 20
countries). Furthermore, the problem with the findings of Allentoft et al. (2015) is that
lactose tolerance frequency was determined only indirectly (based on the presence of
mutations that accompany −13910 * T today). Mathieson et al. (2015a) could not find any
trace of −13910 * T in the available Yamnaya samples and the oldest sample containing
−13910 * T belonged to a man from the Bell Beaker culture (ca. 2300 BC). In any case,
irrespective of the origin of −13910 * T, its frequencies started to increase markedly as
late as the period after its emergence in Central Europe and all the above mentioned
models are not mutually exclusive. When the available data on lactose tolerance from
Europe are combined with those from North Africa, Asia and Oceania, they correlate highly
with dairy proteins (r = 0.80; p < 0.001 in 44 countries) (Appendix Fig. 23a), but much
less with milk protein (r = 0.39; p = 0.008 in 44 countries) (Appendix Fig. 23b). This
counterintuitive finding is in line with the results from Europe. It shows that lactose
tolerance is not a good predictor of the contemporary rates of milk intake, but it is a
fundamental prerequisite for the long-term incorporation of milk products into the diet.
In developing countries, milk usually serves as the main source of high-quality proteins,
irrespective of the lactose tolerance of the local population. Furthermore, it is often
consumed in the fermented form (yoghurt) that retains the biological quality of milk. The
highly developed, lactose tolerant nations of Europe have gradually replaced milk with
more expensive milk products such as cheese. Although cheese and curd contain only casein
(the predominant form of protein in milk), which is of a somewhat lower quality than the
complete milk protein, the advantage of these products lies in the much higher protein
concentration, relative to their volume and energy intake. Not too surprisingly, lactose
tolerance also has a strong relationship with the intake of ‘highly correlated proteins’
(r = 0.80) and animal protein in general (r = 0.75; p < 0.001) (Appendix Table 5e). On the
other hand, it has the most negative relationship with rice protein (r = −0.60; p < 0.001)
and protein from rice and legumes (r = −0.62; p < 0.001). Similar results are reported by
Blum (2013), who suggests that lactose tolerance is a driving force of high animal protein
intake. In Europe, lactose tolerance by itself strongly predicts male height (r = 0.71; p
< 0.001) and its predictive power remains significant even after controlling for all the
other factors that we examined, except its own genetic signature (I-M170 & R1b-U106). This
suggests that the genes for lactose tolerance are associated with some genes that
determine tall stature in Europeans. Indeed, the sudden introduction of ‘tall genes’ into
Central Europe during the Late Neolithic/Early Bronze Age is apparent even in the
paleogenetic analysis conducted by Mathieson et al. (2015a). In our present extended
sample, lactose tolerance also has a strong positive correlation with male height in 47
countries (r = 0.80; p < 0.001) (Fig. 10d). Its significance as a correlate of male height
is retained even after controlling for all the other variables, except ‘highly correlated
proteins’ (p = 0.11). Nevertheless, it is paradoxical that Y haplogroup J1-M267 is
associated with both lactose tolerance and shorter stature. All we can say is that with
the exception of Kuwait and the UAE, the consumption of milk and other dairy products in
the Arabian Peninsula is currently low and lactose tolerance thus does not bring any
practical benefits.

<hs>  Genetics: South, Southeast and East Asia, and Oceania</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Another analysis of Y haplogroups was performed for South, Southeast and East Asia, and
Oceania. We found that the correlations of Y haplogroups with male height in these regions
are generally weak, but they markedly increase, after countries with negligible
frequencies (2% >) are excluded. In this case, O1-MSY2.2 (r = −0.33; p = 0.20 in 17
countries), O2-P31 (r = −0.26; p = 0.37 in 14 countries) and O2a-PK4 (r = −0.43; p = 0.17
in 12 countries) tend to correlate with shorter statures. Only the combination of O1 & O2a
reaches significance (r = −0.53; p = 0.017 in 20 countries) (Fig. 11a). In contrast,
O3-M122 is significantly associated with taller statures (r = 0.42; p = 0.042 in 24
countries) (Fig. 11b). Interestingly, it is O3, not O1 that dominates in the tall
Austronesian speakers of Oceania.

<hs>  Regression analysis of the total sample</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As already stated above, only 72 countries with the complete data for the 38 variables
were used for the multiple regression analysis (Table 3b). To obtain the simplest
predictive model, only four nutritional variables that were significant in the bivariate
correlations were selected: ‘Highly correlated proteins’, poultry, rice (or rice &
legumes), and total energy intake. Protein sources with daily intakes below 5 g/day were
eliminated, similarly like largely duplicit items strongly related to ‘highly correlated
proteins’ (total protein, animal protein, meat total) and plant proteins with a
curvilinear relationship with height. Among the socioeconomic variables, we excluded only
the human development index, because it is characterized by the strongest degree of
collinearity. A separate regression with nutritional variables (Table 4) shows that when
merely two items are considered, by far the highest percentage of variation (adj. R2) is
explained by the combination of ‘highly correlated proteins’ with rice (79.5%), or with
rice & legumes (79.0%). Only total energy intake slightly improves this model (to 80.9%
and 81.5%, respectively)24. Out of all the socioeconomic variables, total fertility
(86.3%) and children's mortality (85.1%) have the biggest additive effect, while
urbanization influences the model only marginally (82.1%). The GDP per capita, health
expenditure per capita and Gini index decrease it very slightly. Nevertheless, the best
model explaining 87.2% of the variation was achieved via the combination of 7 variables.
When we conducted a similar analysis with 83 countries, excluding the Gini index (for
bivariate correlations, see Appendix Table 8), we obtained practically the same results,
with only slightly lower adj. R2 values (Appendix Table 9). In all these models, rice (or
rice & legumes) is the only variable that always retains a very high level of significance
(p < 0.001). These findings point to rice as the most negatively correlated dietary
factor, more so than wheat, which is somewhat unexpected. Although rice is a source of
low-quality protein, similar to other cereals, it has a higher amino acid score, that is,
a higher protein quality than wheat flour (0.63 vs. 0.48 according to the FAO standard
1985). Since rice protein correlates negatively not only with wheat protein (r = −0.69; p
< 0.001), but even with many sources of high-quality animal proteins, especially total
dairy (r = −0.66), ‘highly correlated proteins’ (r = −0.62; p < 0.001), and even total
protein (r = −0.56) and total energy (r = −0.51, p < 0.001), it could be assumed that high
rice consumption symbolizes a diet with a low content of milk and other important
foodstuffs, and reflects general malnutrition. This conclusion could also indicate that
rice reflects general poverty, but the preference for rice or wheat apparently bears no
close relation to the national GDP per capita (Appendix Figs. 24a and 24b) and rice is
even more expensive to harvest than wheat25. Furthermore, the same strong polarity between
height and rice/wheat that was documented in our sample of 93 countries exists in India
and China (Appendix Figs. 25a–25d and 26a–26d). Rice and wheat do not show any significant
association with the GDP per capita in 29 Indian states and 30 Chinese provinces, but rice
correlates significantly negatively with male stature both in India (r = −0.62; p < 0.001)
and China (r = −0.41; p = 0.024). In contrast, wheat shows a positive relationship with
male stature in India (r = 0.53; p = 0.003) and tends to have the same effect in China (r
= 0.25; p = 0.19). Wheat and rice correlate strongly negatively with each other,
especially in China26. Therefore, it is not poverty per se, but mainly geography that
influences rice consumption, because rice-producing regions are unsuitable for the
cultivation of wheat (and vice versa). On the other hand, we should also explain, why the
intake of protein and energy in poor, wheat-consuming nations is much higher than in
comparably poor, rice-consuming nations (Appendix Figs. 10a and 24c). In Vietnam, living
in a farming community and having a lower socioeconomic status are the main determinants
of a low energy intake and high carbohydrate consumption, the latter being directly
related to rice (Nguyen et al., 2013). This points to limited food alternatives in
isolated, poor farming regions of tropical Asia, which are not suitable for large-scale
production of both wheat and livestock. Indeed, another important factor from the World
Bank database, arable land (% of land area, 1993–2009)27, has the most positive
relationship with the consumption of protein from beef (r = 0.42; p < 0.001) and milk (r =
0.41; p < 0.001) in 93 countries, and it is also positively tied to ‘highly correlated
proteins’ (r = 0.34; p < 0.001), total protein (r = 0.23; p = 0.029) and wheat protein (r
= 0.21; p = 0.048). On the other hand, it correlates most negatively with proteins from
rice & legumes (r = −0.31; p = 0.003), rice protein (r = −0.27; p = 0.008) and legume
protein (incl. soy) (r = −0.27; p = 0.009). In accordance with this finding, the
consumption of milk and and the consumption of wheat in India are strongly associated with
each other (r = 0.81; p < 0.001 in urban areas, r = 0.73; p < 0.001 in rural areas).
Furthermore, when the complete data from 72 countries are considered, the socioeconomic
factor with the strongest (negative) relationship with rice is urbanization (r = −0.57; p
< 0.001), which also indicates the influence of narrow food choices. Still, the lack of
other food alternatives in the farming communities of tropical Asia cannot explain, why
the maximum consumption rates of rice protein in the FAOSTAT database (∼30 g/day) are much
lower than those of wheat protein (∼50 g/day). One possible explanation, already outlined
above (see Appendix Fig. 21), is that rice is characterized by a very low nutrient
density. The content of protein in rice is much lower than that in wheat28 and when
protein digestibility (PDCAAS score) is taken into account, roughly 24% more energy from
cooked white rice must be consumed per gram of complete protein, when compared with wheat
flour, in addition to the weight being nearly 4-times greater29. The data from the Czech
Nutridatabaze.cz indicate even greater differences (43% more energy) between white bread
and husked parboiled rice30. Therefore, rice may not only further exacerbate the negative
effect of a low total protein and energy intake, but its high consumption may also
directly contribute to it31.

<hs>  Residuals of observed and predicted height in the total sample</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The comparison of observed and predicted height (Table 5 and Fig. 12a and b), based on
model (10) from Table 4, shows that the region of tropical Asia is characterized by a
clear tendency towards shorter heights than the model predicts (−0.5 cm). Furthermore,
after the exclusion of the outlier urban sample from Laos, the difference rises to −0.8
cm. In contrast, China and South Korea are above the predicted value. Apparently, these
results are compatible with the presumed relationships between height and various
subbranches of Y haplogroup O-M175 in East and Southeast Asia, although the supposed
genetic impact would be relatively small. The influence of genetics in North Africa and
the Near East also appears to be plausible, when only nutrition is considered, but it
diminishes markedly after socioeconomic factors are taken into account. Perhaps the most
interesting observation is thus the position of five Altaic-speaking nations of Central
Asia, which are consistently below the predicted value (−2.0 cm on average). Not too
surprisingly, countries from Western and Southwestern Europe have negative residuals,
whereas positive residuals are generally the most prevalent in the Western Balkans and
Central/Northern Europe (as much as +6.3 cm in Bosnia and Herzegovina, +3.6 cm in Croatia
and +3.1 cm in the Netherlands). Without the Gini index, we again get very similar results
(Appendix Table 10 and Appendix Figs. 27a and 27b), but this time we can even assess
Oceania and more Muslim countries. Interestingly, three countries from Remote Oceania
(Fiji, Kiribati, Samoa) are considerably above the predicted height, and the positive
residual in Samoa reaches +4.2 cm. Two countries from Near Oceania (the Solomon Islands,
Vanuatu) do not come close to these values.

<h>CONCLUSION</h>
----------

The current study extends our previous data from Europe and enables a better understanding
of the enviromental determinants of physical growth in the developing world. The most
fundamental finding is that the nutritional correlates of male height in North Africa,
Asia and Oceania are very different and primarily depend on protein quantity, not protein
quality. Furthermore, three basic nutritional styles can be distinguished, depending on
the major source of protein: The first nutritional style (in tropical Asia) is based on
rice and is also characterized by a very low consumption of protein and energy. It is
accompanied by very small statures between 162 and 168 cm. The second one (in the Muslim
countries of North Africa and the Near East) is based on wheat and the consumption of
plant protein reaches the highest values in the world. The intake of total protein and
total energy is relatively high as well and comparable with Europe, but the average height
of young males is still rather short and does not exceed 174 cm. The third one is based on
animal proteins (particularly those from dairy) and is typical of Northern/Central Europe.
This region is characterized by the tallest statures in the world (>180 cm), being matched
only by the inhabitants of the Western Balkans, in which we can presume extraordinary
genetic predispositions. These world patterns in protein consumption have already been
described in detail by Grigg (1995). Although our present study is based on a non-
experimental, ecological comparison, its findings can provide useful insights into the
relationship between these nutritional styles and the final adult stature. Most
importantly, our results indicate that plant-based diets are not able to provide the
optimal stimuli for physical growth, even if the intake of total protein and total energy
poses no problem. In fact, we observed a difference of 10 cm (174 cm vs. 184 cm) between
nations relying on the surplus of plant and animal proteins, respectively32. A low
consumption of proteins that correlate highly with height can explain the seemingly
perplexing, small stature in the developed countries of East Asia and the Muslim oil
superpowers. Besides low protein quality, a frequently forgotten limiting factor of plant-
based diets is their low nutritional density, with a disproportionate load of ‘empty
calories’ from starch and oils that must be consumed per unit of a key nutrient. The
countries with the highest plant protein intake already belong to the most obese in the
world, particularly among females33, so it is not likely that the deficit of protein
quality could easily be compensated by protein quantity. Last, but not least, our study
can potentially question the current dietary recommendations regarding the intake of
essential amino acids, because some foods that score highly according to the new FAO
standard 2007 do not appear among the best correlates of height. In fact, recent studies
indicate that even the contemporary total protein requirements for children are
underestimated (Elango et al., 2011)34, which also agrees with our data, because we do not
observe any levelling-off in many graphic comparisons of male height and protein
consumption. Of all other variables examined in this study, the human development index
(HDI) is the only factor that shows a comparably strong relationship with male height like
to nutrition. This indicates that the factors leading to the increase in the average
height intertwine with public policies that improve the overall quality of life. As in our
previous study, children's mortality (i.e. a disease free environment) is the strongest
correlate of stature among all the remaining socioeconomic indicators, but the forward
stepwise regression also highlights the role of a lower total fertility rate (i.e. the
amount of resources that can be expended per child) and partly urbanization as additional
factors that can be targeted, when trying to speed up the pace of the positive height
trend. Besides that, our study shows that, similar to the situation in Europe, the final
height in non-European regions may be influenced by genetic factors. Their role in North
Africa and the Near East appears to be similarly strong like in Europe, and the inverse
relationship between height/lactose tolerance in this region is intriguing. The results
are less persuasive concerning the southeastern part of Asia and Oceania, but genetic,
socioeconomic and nutritional data from many local countries are still lacking. In any
case, the verification of these findings is possible only via studies of autosomal DNA.


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<ART>Matching, sorting and wages
===========================

Authors: Jeremy Lise, Costas Meghir, Jean Marc Robin
DOI: 10.1016/j.red.2015.11.004
Year: 2016  |  Pages: 63-87
ASJC codes: 2002
Keywords: Mismatch, Search-matching, Sorting, Wage dynamics

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We develop an empirical search-matching model which is suitable for analyzing the wage, employment and welfare impact of regulation in a labor market with heterogeneous workers and jobs. To achieve this we develop an equilibrium model of wage determination and employment which extends the current literature on equilibrium wage determination with matching and provides a bridge between some of the most prominent macro models and microeconometric research. The model incorporates productivity shocks, long-term contracts, on-the-job search and counter-offers. Importantly, the model allows for the possibility of assortative matching between workers and jobs due to complementarities between worker and job characteristics. We use the model to estimate the potential gain from optimal regulation and we consider the potential gains and redistributive impacts from optimal unemployment benefit policy. Here optimal policy is defined as that which maximizes total output and home production, accounting for the various constraints that arise from search frictions. The model is estimated on the NLSY using the method of moments.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Labor market imperfections may justify labor market interventions. Within a competitive
framework regulation would be welfare reducing, as it would typically reduce employment
and increase insiders' wages. By contrast, any friction constraining the allocation of
workers to jobs inevitably allows some agents to appropriate a greater share of the rent
than a central planner would deem fit. Indeed, if there are important complementarities in
production, mismatch may produce substantial welfare losses relative to the first best or
a constrained planner. We develop a search-matching model in which workers with different
abilities are assigned to different tasks. Our model combines elements from key papers in
the equilibrium search literature. Thus we allow for endogenous job destruction because of
productivity shocks, drawing from the seminal paper of Mortensen and Pissarides (1994). To
this framework we introduce two sided heterogeneity with potential complementarities
between job and worker productivity following Shimer and Smith (2000). In this way we can
investigate sorting in the labor market, one of our motivating interests. To account for
job-to-job transitions and to better explain wage growth we allow for on-the-job search,
which is not present in Shimer and Smith (2000). Wage determination is drawn from Postel-
Vinay and Robin (2002), Dey and Flinn (2005) and Cahuc et al. (2006). In other words we
combine bargaining over the surplus (for workers out of unemployment or moving to a new
job) with Bertrand competition when a poaching firm is involved. In this way, our model
provides a bridge between an essentially theoretical literature on allocation of
heterogeneous workers to jobs,1 and the large microeconometric literature on job mobility
and wage dynamics.2 The framework that we develop allows for frictions and inefficiencies
in the labor market. The frictions are due to the time it takes to locate jobs, which
means that individuals will spend time searching for a job while unemployed and if working
they are likely to be mismatched (if there are complementarities in production). One may
argue that such frictions are inevitable; nevertheless it is important to understand the
welfare loss that they cause relative to the benchmark of a frictionless economy, because
this provides a measure of how dominant search frictions are in determining economic
outcomes.3 More importantly, our model can quantify the welfare loss from inefficiencies
that can potentially be addressed by labor market regulation: first, the number of job
seekers cause congestion making it harder for others to find jobs – this is a standard
externality in models with endogenous arrival rates. Beyond that the potential
complementarities between worker and firm productivities, the possibility of on-the-job
search and the lack of commitment on the worker side allows for the possibility of another
inefficiency: workers and jobs are sometimes willing to form matches whose flow output is
lower than the combined cost of a vacancy and the lost out-of-work benefit. On the one
hand the job, with its local monopsony power manages to extract sufficient surplus to make
it worth hiring the worker; on the other hand the worker prefers the resulting current
loss to the increased flow of income when out of work because being in a job provides a
better outside offer to negotiate a wage once an alternative offer arrives. These features
may be important in the labor market and our model can quantify their importance for
welfare. However, Eeckhout and Kircher (2011) strongly argue against the possibility of
identifying assortative matching in labor markets by this approach, bias-corrected or not.
This is because the surplus of a match is not a monotonic function of worker and firm
characteristics in general. Depending on the distribution of matches around the optimal,
Beckerian allocation, a positive or a negative AKM correlation can be estimated
irrespective of the sign of the correlation between workers' and firms' true unobserved
characteristics in the population of active matches. In the previous working paper we also
find that the AKM correlation is misleading and demonstrate that positive sorting with
respect to unobserved characteristics may induce a negative correlation in the worker and
firm effects estimated on a panel of wages. Lopes de Melo (2009), Hagedorn et al. (2012),
Bagger and Lentz (2014) reach similar conclusions with different models. Note that this
argument invalidating a structural interpretation of AKM is implicit in Gautier and
Teulings (2006), who estimate a regression model of log wages on a quadratic function of
worker and employer types. These types are calculated by projecting log wages separately
on workers' and employers' observed characteristics. Gautier and Teulings's estimation
rests on various parametric restrictions, but nevertheless convincingly claims 1) that the
wage equation is nonlinear in workers' and employers' types, and 2) that they are
positively correlated. Identification of complementarity and sorting, given that we use a
panel of workers' wages and labor market transitions extracted from the NLSY,5 is also
hard to prove or disprove theoretically. However, we argue that sorting can be seen in the
way wage and employment mobility vary as a function of the length of time spent working
following an unemployment spell. Due to search frictions, the cohort of workers entering
the labor market following a spell out of work will start off mismatched, but through on-
the-job search they will become better and better matched with time spent in the labor
market. If the tendency to sort in equilibrium is strong this will result in wages
spreading out as workers sort themselves. Monte Carlo simulations for the Simulated Method
of Moment estimator that we have implemented here seem to suggest that the set of moments
we match do identify the degree of sorting. We find that the NLSY data are best fitted by
our model assuming no complementarity and zero sorting for workers with high-school
education or less and positive complementarity and sorting for college-graduates.6
Finally, our model offers an empirical framework for understanding employment and wage
determination in the presence of firm–worker complementarities, search frictions and
productivity shocks. As a result it offers a way for evaluating the extent to which
regulation may be welfare improving and can evaluate the impact of specific policies such
as unemployment benefit. In a search framework with match complementarities unemployment
benefit can have ambiguous effects on employment and total output. On the one hand, it
allows workers to be more picky and form better matches, which comes at the cost of longer
unemployment spells and higher unemployment. On the other hand, the fact that higher
quality matches will be formed may induce firms to create more jobs, increasing the
contact rate and potentially reducing unemployment duration. Our framework allows this
effect to be quantified (see also Acemoglu and Shimer, 2000). And, in addition, it allows
us to analyze the effect of such policies on the distribution of welfare thus showing who
pays and who benefits from such a policy in this non-competitive environment. We find that
the degree to which labor market interventions are justified depends on whether we are
looking at the low or high skilled markets. Our finding that the market for unskilled
labor (high school graduates or less) is characterized by an extremely low degree of
complementarity implies that mismatch is not very costly. If we reallocated the employed
workers in this group optimally the difference in (steady state) welfare would be 1.1
percent. On the other hand, among the college graduates, optimally reallocating the
employed workers produces a difference in (steady state) welfare of 6.8 percent. We also
find that search frictions are significant. If we do the same experiment with full
employment the welfare changes are 7.8 and 19.6 for the high school and college groups
respectively. The interaction of search frictions and the cost of mismatch (the degree of
complementarity) differ between the two labor markets, implying that a social planner who
is constrained by these friction could attain a welfare increase of 2 percent for the high
school group but only 0.7 percent for the college group, largely by trading off the level
of employment against the cost of creating vacancies. Finally, we find that if we limit
the planner to an optimal unemployment benefit program, this can go a long way to
realizing the potential welfare gains for the high school group. However, it is
ineffectual for the college educated group as the resulting employment distortions
outweigh the gains from improved match quality. The paper proceeds as follows. Section 2
describes the model, Section 3 and Section 4 present the estimation procedure. Sections 5
and 6 describe the data and the choice of moments. Section 7 presents the results of
estimation, analyses the fit and discusses estimation of the degree of sorting. Section 8
presents the welfare analysis, the cost of search frictions, and analyses in detail the
optimal unemployment benefit policy. Section 9 concludes.

<h>THE MODEL</h>
---------

We build a model of individual employment and wage dynamics, with heterogeneous workers
and jobs and with productive complementarities at the match level. This model draws from
Mortensen and Pissarides (1994), as far as the process of match creation and destruction
is concerned, and from Postel-Vinay and Robin (2002), Dey and Flinn (2005) and Cahuc et
al. (2006) in order to incorporate on-the-job search in the Mortensen–Pissarides model. In
addition, we draw from Postel-Vinay and Turon (2010) the renegotiation mechanism for wages
following firm-level productivity shocks. The wage dynamics follow from the process of
search and matching and from firm-level productivity shocks, but entirely abstract from
human capital accumulation and idiosyncratic ability shocks. While important,
incorporating human capital accumulation would complicate matters beyond the scope of this
paper.7

<hs>  Meetings and match formation</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Individuals and jobs are risk neutral and we assume efficiency, in the sense that any
match where the surplus is positive will be formed when the worker and the job meet. Under
these conditions we can characterize the set of equilibrium matches and their surplus
separately from the sharing of the surplus between workers and jobs.

<hs>  Wages</hs>
  ~~~~~

Different wages are negotiated when leaving unemployment, upon poaching, or after a shock
to the job productivity.

     <hss>Poaching</hss>

        Wages can only be renegotiated when either side has an interest to separate if
        they do not obtain an improved offer, assuming that the match remains viable for
        both parties. The events that can trigger renegotiation occur when a suitable
        outside offer is made, or when a productivity shock changes the value of the
        surplus sufficiently. We consider first the impact of an outside offer. In our
        approach there is an asymmetry between workers and firms because the latter do not
        search when the job is filled. As a result they do not fire workers when they find
        an alternative worker who would lead to a larger total surplus, nor do they force
        wages down when an alternative worker is found whose pay would imply an increased
        share for the firm. We decided to impose this asymmetry because in many
        institutional contexts it is hard for the firm to replace workers in this way.
        Moreover, we suspect that even when allowed firms would be reluctant to do so in
        practice. We do, however, allow firms to fire a worker when the current surplus
        becomes negative and then immediately search for a replacement.

     <hss>Productivity shocks</hss>

        Note that a firm hiring an unemployed worker offers the value of unemployment plus
        a share of the surplus, whereas after a positive shock to the surplus value there
        is no Nash bargaining. This may seem both ad hoc and inelegant. However, consider
        the other situation when the match surplus falls below the worker surplus at
        current wage. Under Nash bargaining the worker would get the same share of the new
        surplus as in the other triggering situation, wiping out any wage gains due to
        outside offers. That does not sound right. Intuitively, the worker should have
        more bargaining power in one case than in the other. Our assumption (zero
        bargaining power when the worker values falls below the value of unemployment;
        full bargaining power when the firm profit falls below the value of a vacancy) may
        seem a bit extreme, but it is motivated by the idea that the worker's bargaining
        power should depend on whether renegotiation is wanted by the worker or the
        employer, and it ensures that the value function of the worker is monotonically
        increasing in the wage. Furthermore, wages respond to job specific productivity
        shocks, but not always in an obvious direction. Separations and pay changes may
        happen following both good shocks that increase the value of productivity y and
        bad shocks that decrease it. It is all about mismatch: what matters is what
        happens to the overall surplus. A positive productivity shock, for example, can
        imply that the quality of the match becomes worse and the surplus declines, since
        the outside option of the firm has changed and it may be worthwhile to separate
        from the current worker and post a vacancy to find a better worker. Conversely a
        negative productivity shock can improve the surplus if this means the job type is
        now closer to the optimal one sought by the worker. A shock that reduces the
        surplus can still lead to a wage increase to compensate the worker who is now
        matched with a job with fewer future prospects of wage increases. Thus what really
        matters as far as the viability of the match and the possible options for
        renegotiation is whether a shock improves or worsens a particular match, measured
        by whether it leads to an increase or a decrease, respectively, of the surplus.

<hs>  Value functions</hs>
  ~~~~~~~~~~~~~~~

The next step in solving the model is to characterize the value functions of workers and
jobs, which have been kept implicit up to now. These define the decision rules for each
agent. We proceed by assuming that time is continuous.

     <hss>Employed workers</hss>

        On the right hand side the first term is the wage net of the flow value of
        unemployment (all in parentheses). The second term is the expected excess value to
        the worker of a productivity shock (times the probability that it occurs): in this
        case the worker either ends up with the entire new surplus or the new value or
        indeed nothing if the match is no longer feasible (see equations (7) and (8)). The
        third line is the expected excess value following an outside offer as in equation
        (5). The integral is over all offers that can improve the value (whether the
        worker moves or not).

     <hss>Steady-state flow equation</hss>

        This equation defines the steady-state equilibrium, together with the accounting
        equations (1) and (2).

     <hss>Free entry</hss>

        Appendix B provides a simple iterative algorithm that uses these equations and
        that of the surplus to compute the equilibrium objects.

<hs>  Measurement error</hs>
  ~~~~~~~~~~~~~~~~~

In our model wages are stochastic because of the type of firm that an individual may
encounter, the outside offers or the layoffs that may occur and the productivity shocks.
There will also be unexplained variation due to her productivity characteristic x. In the
data an additional source of variation is measurement error that we need to account for,
so as not to bias the other sources of variation. We use the monthly records of wages in
the NLSY. Thus, while it may be reasonable to assume that measurement error is independent
from one year to the next it may not be so within the year, as all records are reported at
the same interview with recall. Having experimented with a number of alternatives,
including a common equi-correlated component across all months, we settled on a
measurement error structure that is common within year and independent across years. The
variance of measurement error, which is assumed to be lognormal, is estimated alongside
the other parameters of the model.

<h>ESTIMATION METHOD</h>
-----------------

The simulated moments are not necessarily a smooth function of the parameters, although
they would become so as the number of simulations increased to infinity. However, with any
finite and relatively small number of simulations derivative based methods are not
appropriate for finding the minimum. We thus use a method developed by Chernozhukov and
Hong (2003), which does not require derivatives of the criterion function. They construct
a Markov chain that converges to a stationary process of which the ergodic distribution
has a mode that is asymptotically equivalent to the SMM estimator. Appendix C describes
this procedure in detail.

<h>THE DATA</h>
--------

We use the 1979 to 2002 waves of the National Longitudinal Survey of Youth 1979 (NLSY).
The NLSY consists of 12,686 individuals who were 14 to 21 years of age as of January,
1979. It contains a nationally representative core random sample, as well as an over-
sample of black, Hispanic, the military, and poor white individuals. For our analysis, we
keep only white males from the core sample. We only include data for individuals once they
have completed their education. We also drop individuals who have served in the military,
and follow workers up to the point of a non-employment spell of 36 months or longer. We
consider these workers to have left the labor force. We subdivide the data into two
education groups: high school degree or less, and college graduate. The model is estimated
separately on these subgroups. Individuals are interviewed once a year and provide
retrospective information on their labor market transitions and their earnings. From this
we construct histories at a monthly frequency aggregating the data as follows: we define a
worker as employed in a given week if he worked more than 35 hours in the week. We define
a worker's employment status in a month as the activity he was engaged in for the majority
of the month, treating unemployment spells of two weeks or less as job-to-job transitions.
After sample selection, we are left with an unbalanced panel of 2125 individuals (446,747
person months). We remove aggregate growth from wages based on average wage growth in
years 10 to 20 from completion of education. At this point the main source of wage growth
is due to aggregate productivity. Having removed this constant growth rate from wages we
assume that the remaining growth is attributable to gains from job search.11 Finally, we
trim the data to remove a very small number of outliers when calculating wage changes.
When calculating month to month wage changes, we exclude observations where the wage falls
by more than half or increases by more than a factor of five.

<h>CHOICE OF MOMENTS AND IDENTIFICATION</h>
------------------------------------

The model will be estimated based on worker level data recording transitions between jobs
and between work and unemployment as well wages over time. We have no information on the
firm side itself (such as for example productivity). As such identification is
challenging. Lamadon et al. (2014) discuss the formal non-parametric identification of a
model similar to this, albeit without productivity shocks and using matched employer
employee data. Other insightful work with more formal discussion of identification is
Hagedorn et al. (2012), who analyze a version of the model without on-the-job search, and
Bagger and Lentz (2014), where sorting results from heterogeneous search strategies. The
key result is that the complementarities in the worker–job match can be identified
nonparametrically in their context, using job-side information on productivity and job
duration. Here we present a heuristic description of the identification argument based on
the simpler data at our disposal and using a specific parametric form for the match
production function. Transitions in and out of work and between jobs play a key role in
parameters controlling labor market mobility. In particular η (matching efficiency) and s
(relative search intensity) that help determine the arrival rate of offers are identified
by exit from unemployment and by mobility between jobs. Exit from employment is governed
by two components of the model: productivity shocks to the job and the exogenous
destruction rate. However, productivity shocks are also related to job-to-job transitions
and wage growth and cannot be set to fit perfectly the exit rate from employment. The
remainder is captured by the exogenous match destruction rate ξ. Changing the distribution
of y and its shocks affects transitions both between jobs and in and out of unemployment.
In addition, changing the distribution of x will affect the variance of wage growth in a
very specific way, governed by the structure of pay setting and will also affect
transitions in and out of work. Thus the distribution of these objects is intimately
linked to observed transitions, which will limit the extent to which we can explain the
variance of wages and their growth. We thus identify the variance of measurement error in
wages from the variance of wages that the economic model is unable to reproduce.
Identification of the model in practice requires a careful choice of moments that will be
sensitive to the parameters we need to estimate. In particular, to summarize the
employment dynamics, we use the long-run employment rate and the transitions between
employment states and between jobs, calculated on years 16–20. To summarize wage dynamics,
we include the level of (log)wages and their cross sectional variance as well as wage
growth and its variance both within and between jobs. Each of these moments is calculated
separately by year in the labor force (year since leaving school for the cohort). All the
moments we use, their values in intervals of five years and the value produced by the
model are shown in Table 4. In addition, we target the mean vacancy to unemployment rate
(based on the mean and standard deviation from Hagedorn and Manovskii, 2008).

<hs>  The fit of the moments</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

Summaries of the fit of the targeted moments by the model are presented in Table 4. As
seen from the table the transitions rates are fitted remarkably well. In Figs. 1 and 2 we
summarize the fit of the model for wages, wage growth and the corresponding variances,
both overall and by type of transition for the lower and higher education individuals
respectively. The model generally fits these patterns very well and certainly captures the
qualitative features of the data.13 Any wage growth generated by the model is due to the
job search process and reflects mobility towards better jobs and (for the higher educated
people) improvements in sorting. For the lower educated people as we shall see there are
very few complementarities; however as the workers move to higher surplus jobs (because of
improved firm productivity) and by receiving outside offers they can improve their wage.
This process of outside offers is responsible for the observed wage growth for the low
skilled.

<hs>  Parameter estimates</hs>
  ~~~~~~~~~~~~~~~~~~~

The complete set of parameter estimates is presented in Table 5. Here we focus on a subset
that have a direct economic interpretation; these are presented in Table 1. The key
parameter of interest is the complementarity parameter (ρ). For lower skill worker this is
close to and indeed not significantly different from one. This implies that there are
practically no complementarities between worker and job characteristics, which appear to
be perfect substitutes. However, for college graduates the elasticity of substitution is
about 0.53 implying a high degree of complementarity and hence large gains from sorting.
The gains from moving up the job ladder are thus much more important for college graduates
than for those with lower levels of education. However, as mentioned above, the unskilled
can still gain from outside offers: first, search frictions will imply a surplus, since
the departure of the worker will mean the job will remain idle for some time and hence the
firm will have an incentive to match outside offers from jobs with lower surplus. Second,
the surplus is increasing in job productivity y but (almost) not in worker productivity x.
This is because the cost of a vacancy is constant but the flow of out-of-work income is
increasing in x (see equation (13)). Hence higher productivity firms can afford higher
wages. The way the surplus is split is driven by the Nash bargaining parameter β. This is
slightly higher for college graduates than for unskilled workers. The former obtain 27% of
the surplus while the unskilled about 18%. Turning now to the parameters governing search,
the search intensity (s) for the employed workers is a third of that for those out of work
among the low education group and half that among the college graduates. Effectively this
means that the rate of arrival of job offers is much higher for those out of work and this
has an implication on what jobs the unemployed are willing to take. The implications of
the parameter estimates of the search technology (η and s) are better understood by
calculating the probabilities of a job contact when employed and unemployed, which are
displayed in Table 2. The contact rates for the unskilled when unemployed are lower than
for the higher skilled (17.1% compared to 23.1%). However the unskilled accept all offers
when unemployed. Both the contact rate when working and the rate at which alternative
offers are accepted declines with skill.

<hs>  Sorting in the labor market</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~

The complementarities between worker and job characteristics for the higher education
group imply perfect assortative matching in a first best world. However, the extent of
sorting that occurs in practice depends on the importance of frictions. In Fig. 3 we
summarize the sorting patterns in the decentralized equilibrium, as implied by our point
estimates of the parameters. The lines in the figure are contours of the surplus function.
On each contour the surplus is constant and non-negative, for various combinations of
worker and job productivities. In the left hand panel, corresponding to the low education
workers, such lines cover the entire support of the distribution of worker and firm
characteristics. This reflects the fact that all matches are viable, leading to a non-
negative surplus, because of the almost complete absence of complementarities.16 In the
right hand panel, relating to college graduates, the upper-left and lower-right sections
have no contours: these areas represent combinations of worker and job types where the
surplus is negative and no matches ever occur.17 Waiting for a better match has higher
value than starting to produce. For low skill workers over most of the space the contours
are downward sloping. This points to a trade off between firm and job characteristics at a
fixed match surplus. However, for college graduates the contours are mostly upward sloping
(except at the highest levels of skills and job characteristics). This is because, when
complementarities are very important an increase in the job productivity requires an
increase in the human capital of the worker if the surplus is to remain constant, rather
than decline. As an example of the matching process consider a college educated worker at
the 50th percentile of the x distribution. The surplus initially increases in the type of
the job, is maximized when matched to a job at the 50th percentile, and then declines
again. This worker will initially match with any job above the 15th percentile, but will
always move to a job that is closer to the 50th percentile, which may involve moving up or
down the quantiles of y. Fig. 4 illustrates sorting within the College educated group by
plotting the distribution of worker (job) characteristics conditional on various
percentiles of the job (worker) productivity they are matched with. Distributions
conditional on higher values of productivity of the counterpart to the match
stochastically dominate those that are conditional on lower values. Moreover, the support
of these distributions is limited to a strict subset of the entire support, reflecting the
fact that some matches never occur. Finally, matches are not uniformly distributed over
this support, even for the low educated. We illustrate the density of matches over the
matching set in Fig. 5. For the college group, as we approach the main diagonal, of
perfect sorting the density of matches increases. For the high school group, all workers
above the 20th percentile move up toward the highest firm type at the same rate. Below the
20th percentile there is some sorting induced by the mild complementarity (for low x-types
the surplus decreases when moving to higher y-type firms, although it is still positive. A
caveat here is that our estimate is not distinguishable from linearity, in which case
there would be no sorting at all for this group.

<h>WELFARE ANALYSIS</h>
----------------

To provide a sense of the potential gains from policy, we consider three thought
experiments. First we take the estimated search frictions as given and look at the
Planner's constrained efficient solution. This experiment provides an upper bound on what
can be achieved by policies that work to eliminate congestion externalities, taking the
frictions as given. Second, we consider the thought experiment of ignoring the search
frictions and solving the frictionless assignment problem. We do this both keeping the
number of employed worker fixed to the estimated level, as well as for the full employment
case, allowing us to separate the employment from the mismatch effects of frictions. This
experiment provides an estimate of the upper bound to the benefits of finding
technological solutions around the frictions (such as improved centralized matching) but
has nothing to say about either the feasibility or costs of such a program. Finally, we
consider an optimal Unemployment benefit program. This experiment provides an estimate of
the potential gain from a feasible policy.

<hs>  The planner's constrained efficient solution</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The potential for welfare-enhancing labor market regulation arises from the job search
frictions and the externalities they cause during the job allocation process. The
externalities arise from the classic issue of “overcrowding” among job seekers, i.e. when
an extra person or vacancy seeks a match it reduces the arrival rate for others as implied
by the matching function. An extra dimension arises in our model because of heterogeneity
and sorting: by having low quality jobs compete for workers they lengthen the time it
takes to fill higher productivity ones, without adding much when they are filled (because
they have zero or near zero surplus).18 This implies that because of complementarity,
cutting some low productivity jobs may increase welfare, even if this means that some very
low productivity workers never work. Any regulatory intervention in the labor market will
improve welfare only to the extent that it can address the externalities discussed above,
and to the extent to which they are significant. Thus, to provide a measure of the
potential welfare gains from labor market regulation (such as in-work benefits,
unemployment benefit, minimum wages, severance pay etc.) we solve the planners problem
respecting the constraints arising from search frictions. Table 3 shows the breakdown of
contributions to total welfare under different scenarios. The first column relates to the
fully decentralized economy we observe from the data. The second column shows the results
of the planner maximizing welfare as in (16). For the lowest education group the
constrained planner is able to improve on the decentralized outcome by two percent. For
the higher education group the planner can attain an increase in welfare of only 0.71
percent. The planner increases unemployment and reduces the number of jobs. To understand
what is going on, note that increased match quality contributes nothing to the welfare
increase. Output per match does not change. The planner increases welfare by reducing
vacancies (which are very costly) and allowing more workers to engage in home production.
For the high school or less group, where there are no complementarities in production,
this reallocation achieves a relatively large increase in welfare. For college graduates,
the welfare gains are much more modest because by reducing the number of vacancies some
high surplus jobs are also eliminated and home production is less effective for this
group. Nevertheless, the reduction of jobs for them is much lower.

<hs>  The costs of search frictions</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In column (4), we run a similar counterfactual in which we assign all jobs to workers.
Unemployment is drastically reduced and welfare increases a lot, largely because there are
no recruiting costs, but also because of reduced unemployment, and a slightly higher match
quality for the lowest education groups (see also the discussion in Subsection 8.3.2).
This experiment indicates that there may be substantial gains from reducing search
frictions: for the lowest skill group policies that improve search technology could
improve welfare by up to 7.8% (19.6% for the college educated group). Part of this
increase comes from reducing unemployment. But part also comes from improving sorting if
we take the point estimate of the elasticity of substitution, which is 16.2. This can be
seen from the third column of Table 3 where unemployment is kept equal to the level in the
benchmark economy and we observe a rise in match quality.

     <hss>Overall efficiency gains</hss>

        For the low education group, optimal unemployment benefit can deliver 1.4% of
        improved welfare, corresponding to 68.8 percent of the potential gains attainable
        by the planner working under the same constraints. This involves increasing the
        baseline flow utility of being out of work (home production) for each individual
        by 11.09 percent of their expected output if employed, and financing this by a tax
        on output of 0.95 percent. The gain is effectively zero for the high education
        group. It is worth noting again that the improvement in steady state output comes
        from very different sources when comparing the elimination of frictions to the
        constrained planner or optimal unemployment benefit scheme. With the removal of
        frictions there is a direct increase in market production and a gain when netting
        out the costs of vacancy creation from home production. For the low education
        group, where the constrained planner can improve steady state output, this is
        implemented largely by raising unemployment and reducing the number of vacancies,
        resulting in lower vacancy creation costs and higher levels of home production,
        but without improving the average quality of productive matches.

     <hss>The redistributive effects of the policy</hss>

        As discussed above, we find that there is a potential aggregate gain from an
        optimal unemployment benefit scheme (although negligible for college graduates).
        In addition to overall efficiency gains, we are also interested in the
        redistributive effects of policy. In an environment with heterogeneous workers it
        is not necessarily the case that an increase in steady state output will benefit
        all workers the same, indeed it may harm some. In Fig. 6 we plot the difference in
        value, by worker type x, between being unemployed in an economy with and without
        the optimal unemployment benefit scheme. While the value of unemployment is higher
        for all worker types in the low education group, it is effectively zero for
        college educated workers above the second quintile. Thus, there are no losers from
        this optimal UI policy, but the gains are concentrated among the low educated as
        well as the lower productivity individuals among the college graduates.

<h>CONCLUDING REMARKS</h>
------------------

We develop an equilibrium model of employment and wage determination, which builds on the
work of Mortensen and Pissarides (1994), Shimer and Smith (2000) and Postel-Vinay and
Robin (2002). In our model both workers and firms are heterogeneous and their productivity
characteristics are potentially complementary in production creating the possibility of
sorting. However, firms are subject to productivity shocks. Workers can search both on and
off the job. This creates an environment where there may be potential for welfare
improving labor market regulation. Moreover our framework is well suited to consider the
redistributive (as well as efficiency) implications of policy. The scope for and impact of
policy is thus an empirical issue in our model. We estimate the model based on NLSY data
and find strong evidence of complementarities between worker and firm characteristics,
leading to sorting for the college educated workers. For this education group these
complementarities imply large efficiency losses due to mismatch between job and worker
productivities caused by search frictions. The complementarities are much weaker for the
low education workers, where the production function is effectively linear in individual
an job productivities. Mismatch is a source of inefficiency that labor market regulation
cannot correct; this would require changing the job search technology, improving job
finding rates and enabling more mobility following shocks. However, we show that the
potential welfare gains from eliminating mismatch and frictions can be as high as 20% for
college graduates and 8% for the lower educated. Policies such as unemployment benefit can
improve efficiency to the extent that they address the externalities induced by search
frictions. We establish that optimal labor market regulation can improve welfare by up to
2% for low skill workers and 0.71% for college graduates. Some 70% of the improvement can
be achieved with optimal unemployment benefit alone for the lower educated individuals,
but such a policy can achieve nothing for the college graduate group. Our model opens up
an empirical research agenda on which to build and address important issues. We
demonstrate the importance of heterogeneity, sorting and search frictions. Among these are
the welfare and labor market effects of risk and the role of assets in determining the
wage offer distribution and the role of investment in human capital. Similarly, an
important extension of such a model is considering investment decisions by firms and how
this can affect productivity y which we took as given. Finally, this kind of model is well
suited to interpreting matched employer employee data. Indeed such data could aid
identification by providing direct information on firm level productivity, and on the
distribution of worker types employed at the same firm type (see Lamadon et al., 2014).
However, when we move to such data new, important and difficult questions arise when
defining wage setting in an environment with sorting and multiple workers per firm. This
is of course an important future area of research.


<h>REFERENCES</h>
----------

  [1] John M. Abowd, Francis Kramarz, David N. Margolis. High wage workers and high wage firms. doi:10.1111/1468-0262.00020
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<ART>Mendelian randomization in health research: Using appropriate genetic variants and avoiding biased estimates
================================================================================

Authors: Amy E. Taylor, Neil M. Davies, Jennifer J. Ware, Tyler Vanderweele, George Davey Smith, Marcus R. Munafò
DOI: 10.1016/j.ehb.2013.12.002
Year: 2014  |  Pages: 99-106
ASJC codes: 2001
Keywords: Causal inference, Instrumental variable, Mendelian randomization, Smoking, Tobacco

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Mendelian randomization methods, which use genetic variants as instrumental variables for exposures of interest to overcome problems of confounding and reverse causality, are becoming widespread for assessing causal relationships in epidemiological studies. The main purpose of this paper is to demonstrate how results can be biased if researchers select genetic variants on the basis of their association with the exposure in their own dataset, as often happens in candidate gene analyses. This can lead to estimates that indicate apparent "causal" relationships, despite there being no true effect of the exposure. In addition, we discuss the potential bias in estimates of magnitudes of effect from Mendelian randomization analyses when the measured exposure is a poor proxy for the true underlying exposure. We illustrate these points with specific reference to tobacco research. © 2013 The Authors.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Proving how exposures affect health outcomes can be problematic in observational studies.
Even if an exposure and an outcome are associated, the direction of causality can be
difficult to ascertain because health outcomes can lead to changes in behaviour which can
affect exposures (Munafò and Araya, 2010). Mendelian randomization studies may help to
shed light on these relationships by using genetic variants, such as single nucleotide
polymorphisms (SNPs) (see Table 1 for definition), as instrumental variables for measured
lifestyle exposures (Davey Smith and Ebrahim, 2003). Mendelian randomization studies can
be used for two related purposes: (1) to provide evidence for the existence of causal
associations, and (2) to enable accurate estimation of the magnitude of the effect of
lifelong exposure to a risk factor on an outcome (Davey Smith and Ebrahim, 2004). As is
the case for instrumental variable methods generally, for Mendelian randomization studies
to be useful genetic variants must be robustly associated with the exposure of interest
(Davey Smith and Ebrahim, 2005; Lawlor et al., 2008b). Despite this, recent Mendelian
randomization studies conducted by Wehby et al. (2011a,b, 2012) have used genetic variants
as instruments for smoking heaviness which were not shown to be associated with smoking
phenotypes in large genome wide association studies. Whilst the authors acknowledge that
these variants have not been consistently associated with smoking phenotypes, they suggest
that the variants provide evidence of causal effects of smoking on body weight (Wehby et
al., 2012) and smoking in pregnancy on birthweight (Wehby et al., 2011b) and risk of
orofacial clefts in offspring (Wehby et al., 2011a). In addition, the authors use the
genetic variants to estimate the magnitude of effect of smoking heaviness on their
outcomes of interest (Wehby et al., 2011a,b, 2012). Even if the variants they use are
truly associated with smoking behaviour, this is likely to produce incorrect estimates of
the effect size of smoking on the outcome.

<hs>  Aims</hs>
  ~~~~

In this paper, we aim: (1) to illustrate, using a data simulation, why inferences based on
the results of Mendelian randomization studies using genetic variants selected based on
their association in a single sample are likely to be misleading and (2) to demonstrate
why estimating the magnitudes of causal effects in cases where the measured exposure is
not the same as the underlying exposure captured by the variant is problematic. We discuss
these issues with reference to the specific case of tobacco as an exposure, but these
principles can be applied more widely to Mendelian randomization and instrumental variable
analyses.

<hs>  Assumptions of Mendelian randomization</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The principle of Mendelian randomization relies on the basic (but approximate) laws of
Mendelian genetics (segregation and independent assortment). If these two laws hold, then
at a population level, genetic variants will not be associated with the confounding
factors that generally distort conventional observational studies (Davey Smith and
Ebrahim, 2003; Davey Smith, 2011). In addition, genetic variants will not be affected by
reverse causality (Davey Smith and Ebrahim, 2003). Epidemiological studies increasingly
use Mendelian randomization to provide robust evidence of underlying causal mechanisms in
a number of areas of health research including cardiovascular disease, cancer and mental
health (Casas et al., 2005; Davey Smith et al., 2005; Benn et al., 2011; Scott et al.,
2011; Interleukin-6 Receptor Mendelian Randomisation Analysis et al., 2012; Nordestgaard
et al., 2012; Voight et al., 2012; Carslake et al., 2013). For a SNP to be a valid
instrumental variable, the following assumptions must hold: (1) the SNP should be reliably
associated with the exposure, (2) the SNP should only be associated with the outcome
through the exposure of interest (the “exclusion restriction”) and (3) the SNP should be
independent of other factors affecting the outcome (confounders) (Angrist et al., 1996;
Lawlor et al., 2008b; Wehby et al., 2008; Clarke and Windmeijer, 2012). Moreover, to use
Mendelian randomization for accurate estimation of effect sizes in mediation analysis
using a measured exposure, the measured exposure should accurately capture the true causal
exposure (Lawlor et al., 2008a; Pierce and VanderWeele, 2012).

<hs>  Genetic variants for tobacco research</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Large consortium-based genome wide association studies have found genetic variants
robustly associated with smoking behaviours (Thorgeirsson et al., 2008; Furberg et al.,
2010; Liu et al., 2010). One genetic variant that has been highlighted by these studies,
amongst others, is located in the nicotinic receptor gene cluster CHRNA5–A3–B4 on
chromosome 15. Two SNPs within this region, rs16969968 and rs1051730, which are in linkage
disequilibrium and can be used interchangeably in studies on Europeans, consistently
associate with measures of heaviness of smoking (e.g., cigarettes per day or biomarkers of
nicotine exposure) (Freathy et al., 2009; Munafò et al., 2012). Smokers with a single copy
of the smoking increasing allele smoke on average one extra cigarette per day compared to
those with no copies. The effects of the SNP are additive, so people with two copies of
the smoking increasing allele on average smoke two additional cigarettes a day (Ware et
al., 2011). The strength and consistency of this association make these variants suitable
instruments for use in Mendelian randomization studies. The second assumption of
instrumental variable analysis, that the SNP should only be associated with the outcome
through the exposure of interest, is rarely fully testable (Glymour et al., 2012). In
Mendelian randomization, this assumption may be violated if the genetic variant has
pleiotropic effects, is in linkage disequilibrium with another variant of differing
function or if its effects are buffered by canalization (Davey Smith and Ebrahim, 2003).
However, the biological function of the nicotinic receptor gene cluster and evidence from
epidemiological studies suggest that this variant is likely to affect outcomes only
through tobacco exposure (for a further discussion of this see Section 3). In addition, if
the variant is associated with an outcome in smokers or former smokers but not never
smokers, this is a good indication that the association is fully mediated through tobacco
exposure (Freathy et al., 2011). The rs1051730 SNP has been used in Mendelian
randomization studies to investigate the causal effect of cigarette smoking on body mass
index, depression anxiety and birthweight of offspring (Freathy et al., 2011; Lewis et
al., 2011; Bjorngaard et al., 2013; Tyrrell et al., 2012). Despite the identification of
variants in the CHRNA5–A3–B4 gene cluster as suitable instruments, Wehby et al. (2011a,b,
2012) use other variants (in DRD2, MAOA, DRD4, 5HTT, GABBR2, CYP2D6) as instruments for
smoking heaviness in their Mendelian randomization studies. The authors justify this
approach by emphasizing the plausible biological roles of their chosen variants in smoking
behaviour. However, this justification is questionable given that the candidate gene
approach for finding functional genetic variants has had limited success, yielding few
replicable associations and many false positives (Colhoun et al., 2003; Sleiman and Grant,
2010; Lawlor et al., 2008b). If these common variants are truly associated with the
exposure, these associations should have been detected in the large genome wide
association studies of smoking behaviour. We calculated that the largest of these studies,
conducted by the TAG consortium, which included 74,000 smokers had 80% power to detect
variants explaining as little as 0.05% of the variance in cigarettes per day (Furberg et
al., 2010). Genetic variation in the CHRNA5–A3–B4 gene cluster explains about 1% of the
variance in cigarettes per day (Munafò et al., 2012).

<hs>  Data simulation</hs>
  ~~~~~~~~~~~~~~~

We next expand our simulation to demonstrate how biases can occur if instruments are
selected based on their observed associations with the exposure in the sample within which
the Mendelian randomization experiment is being carried out. To simulate an example in
which there is no effect of the exposure on the outcome, we set β1 = 0, so the outcome and
exposure were only correlated (correlation = 0.6) due to the error terms. Thus the
association of the exposure and outcome is confounded. This means that if our estimation
model (estimator) is correct, then it should find no effect of the exposure on the
outcome. If our estimator is incorrect and we find a relationship between the outcome and
the exposure, then it suggests our estimator is biased. Next, to simulate the selection of
genetic instruments within a sample, we randomly generated 1000 binary variables (Z) to
simulate the SNPs (all had a frequency of 0.3). Since these instruments were randomly
generated, there was no underlying effect of the SNPs on the exposure (α1 = 0). We used a
binary instrument in a one instrument and one exposure example for simplicity, but these
results are generalizable to additive genetic models or Mendelian randomization studies
using multiple genetic variants (Pierce et al., 2011; Clarke and Windmeijer, 2012). We
estimated the association of each SNP with the exposure, X, using robust linear
regression. As expected, by chance, roughly 5% of these SNPs were associated with the
exposure (using a p-value cut-off of 0.05). We selected the ten instruments most strongly
associated with the exposure and ran a two stage least squares regression on the outcome
using each of these instruments in turn. Table 3 presents the effect sizes and p-values
for the association of the instrument with the exposure and the outcome along with the
F-statistic (a measure of the strength of the association of instrument and exposure). Of
the ten instruments selected, three had an F-statistic above the commonly used cut off
point of 10, suggesting that the associations of instruments and exposure were strong
enough for the instrumental variable estimates to be unbiased (Stock et al., 2002). Using
two-stage least-squares regression, five of the instruments showed strong or moderate
evidence for associations with the outcome (p values <0.01), and two further instruments
were weakly associated (p values <0.1). However, we know that no “true” relationship
exists, because of how we generated the data. Therefore, these instruments, and
specifically how we selected the instruments biased the two-stage least squares estimates
of the effect of the exposure on the outcome. Use of inappropriate genetic variants is not
a problem specific to studies of tobacco research (Fletcher and Lehrer, 2011), but this
example illustrates this problem well because of the availability of good instruments for
smoking behaviour. The importance of this issue more generally in Mendelian randomization
studies has been highlighted previously by Lawlor et al. (2008b) with reference to
smoking- and obesity-related variants.

<hs>  The Beavis effect</hs>
  ~~~~~~~~~~~~~~~~~

Even when a variant discovered in a single sample is truly associated with an exposure,
the effect sizes of variants identified within a single sample are, by the nature of their
discovery, likely to be larger than in the overall population (the Beavis effect, or
Winner's Curse) (Goring et al., 2001; Ioannidis, 2008; Burgess et al., 2011).

<h>BIASES IN MAGNITUDES OF EFFECTS FROM INSTRUMENTAL VARIABLE ANALYSIS</h>
-------------------------------------------------------------------

Mendelian randomization can provide very good estimates of the magnitude of effects of
long term exposure to a risk factor on outcomes (Davey Smith and Ebrahim, 2005; Ference et
al., 2012). However, when the phenotypic exposure of interest (e.g., cigarettes per day)
does not adequately capture the “causal” exposure through which the genetic variant
operates (e.g., lifetime exposure to tobacco), estimates from two-stage least-squares
regression may be biased. In such cases, the second assumption of instrumental variable
analysis (the exclusion restriction assumption) is violated. The genetic variant is still
a valid instrument for the underlying phenotype of interest and can therefore still
provide evidence of causality. However, it is not a valid instrument for the effect of the
measured phenotype on the outcome and so magnitudes of effect are likely to be incorrect
(Glymour et al., 2012). This principle also applies more widely to instrumental variable
analyses using non genetic instruments, but this issue has not been well-developed in the
econometrics or statistics literatures. In tobacco research, self-reported measures of
smoking behaviour (such as number of cigarettes smoked per day) may be inadequate
phenotypes because people smoke cigarettes differently. For example, there is variation in
the number of puffs taken, volume of smoke inhaled or how far down the cigarette is smoked
before it is discarded (Strasser et al., 2007; McNeill and Munafò, 2013). Objective
measures of tobacco exposure (e.g., level of cotinine, the primary metabolite of nicotine)
are likely to provide more valid assessment of actual biological exposure (i.e., the
amount of smoked inhaled). For example, the rs1051370/rs16969968 variants are considerably
more strongly associated with circulating levels of cotinine, than with self-reported
daily cigarette consumption, explaining 4% and 1% of the variance in these phenotypes
respectively (Keskitalo et al., 2009; Munafò et al., 2012). Researchers rarely have data
on phenotypes such as cotinine, and often use a proxy measure such as self-reported
cigarette smoking rates. This issue is illustrated in Fig. 1. We are particularly
interested in the effect (a) of lifetime exposure to tobacco smoke (X) on an outcome
measure (Y) (see Fig. 1A). Unfortunately, we may only have data on cigarettes smoked per
day (X2), which is associated with but does not fully capture lifetime exposure (see Fig.
1B). The raw association of smoking on the outcome is confounded by the unobserved
variable U (the error terms in our simulations). The genetic variant (Z), not only affects
the total lifetime exposure (b), but also the number of cigarettes smoked (c). According
to the second assumption of instrumental variable analysis, Z should only affect the
outcome through its effect on the number of cigarettes smoked per day (X2) but in this
case it also affects the outcome through lifetime exposure to tobacco smoke (X). In the
example above, if we adjust the association of the variant (Z) with the outcome (Y) for
the measured phenotype (X2) we would not expect the association to disappear because Z
still affects Y through lifetime exposure to tobacco smoke (X). This issue has generated
debate in the literature; the residual association observed between the CHRNA5–A3–B4
variants and lung cancer following adjustment for cigarettes per day has led to
suggestions of a direct effect of the variant on lung cancer which does not operate though
smoking (Lips et al., 2010; Wang et al., 2010a). However, Munafò et al. (2012) calculated
that association between the variant and lung cancer was consistent with full mediation
through tobacco exposure if cotinine were used as an intermediate measure of tobacco
exposure rather than cigarettes per day. Therefore, the apparent direct association
between these variants and lung cancer is likely to be a function of poor tobacco exposure
measurement. This has important implications for the use of two-stage least-squares
regression in Mendelian randomization analyses of smoking. If the measured exposure does
not capture all dimensions of the relevant exposure domain, we can still infer a causal
relationship, but cannot obtain an accurate estimate of the effect size of the underlying
causal exposure. Thus the effect sizes presented in papers using cigarettes per day as the
measured exposure of interest are likely to be subject to bias and should be interpreted
with caution. It should be noted that this differs from the issue of random and systematic
measurement error in the exposure phenotype, as discussed by Pierce and VanderWeele
(2012). This is because even if cigarettes per day were measured perfectly, this phenotype
would not adequately capture tobacco exposure. Whilst this is a particular issue for
studies of tobacco use, this is also relevant for Mendelian randomization studies of other
exposures. For example, estimates from Mendelian randomization studies using variants
which affect caffeine consumption may be biased if the measured phenotype is number of
cups of coffee consumed per day because this measure does not account for caffeine content
of each cup. Glymour et al. (2012) also discuss this issue in relation to incorrect
specification of the appropriate causal time period for an exposure, using body mass index
as an example.

<h>CONCLUSIONS</h>
-----------

The results of Mendelian randomization studies, based on genetic variants chosen because
of their association with the exposure in any one sample, do not contribute useful
evidence of the effects of exposures on health outcomes. It is essential for Mendelian
randomization studies to use genetic variants that are robustly associated with the
exposure of interest. Fortunately, this is now possible for a number of exposures,
including tobacco, generally because of variants identified in large genome wide
association studies and replicated in independent samples (Timpson et al., 2005; Frayling
et al., 2007; Hazra et al., 2008; Furberg et al., 2010; Wang et al., 2010b; Voight et al.,
2012). Mendelian randomization studies, as well as establishing causal associations, can
provide good estimates of the magnitudes of effect between exposures and outcomes as they
are free from bias by confounding. However, estimates may be biased if the measured
exposures are not the same underlying exposure as that represented by the genetic variant.
Crucially, even if the underlying causal exposure is perfectly measured, if the variant
additionally affects the outcome through a different pathway, neither causality nor
strength of associations can be estimated. Mendelian randomization has the potential to be
a valuable tool to further our understanding of the aetiology of disease. Researchers will
only realize this potential if they base their studies on well-characterized variants and
are cautious about making inferences about magnitudes of the relationships between
observed phenotypes and outcomes.

<h>FINANCIAL SUPPORT</h>
-----------------

Amy Taylor, Jennifer Ware and Marcus Munafò are members of the UK Centre for Tobacco and
Alcohol Studies, a UKCRC Public Health Research: Centre of Excellence. Funding from
British Heart Foundation, Cancer Research UK, Economic and Social Research Council,
Medical Research Council, and the National Institute for Health Research, under the
auspices of the UK Clinical Research Collaboration, is gratefully acknowledged. This work
was supported by the Wellcome Trust (grant number 086684) and the Medical Research Council
(grant numbers MR/J01351X/1, G0800612, G0802736, G0600705, MC_UU_12013/1-9). George Davey
Smith and Neil Davies are supported by the European Research Council DEVHEALTH grant
(269874). Jennifer Ware is supported by a Post-Doctoral Research Fellowship from the Oak
Foundation. Tyler VanderWeele is supported by an NIH grant (R01 ES017876).


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<ART>Money demand instability and real exchange rate persistence in the monetary model of USD-JPY exchange rate
================================================================================

Authors: John Hunter, Faek Menla Ali
DOI: 10.1016/j.econmod.2014.03.019
Year: 2014  |  Pages: 42-51
ASJC codes: 2002
Keywords: Cointegration, Exchange rates, Monetary model, Weak exogeneity

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper proposes a hybrid monetary model of the dollar-yen exchange rate that takes into account factors affecting the conventional monetary model's building blocks. In particular, the hybrid monetary model is based on the incorporation of real stock prices to enhance money demand stability and also, productivity differential, relative government spending, and real oil price to explain real exchange rate persistence. By using quarterly data over a period of high international capital mobility and volatility (1980:01-2009:04), the results show that the proposed hybrid model provides a coherent long-run relation to explain the dollar-yen exchange rate as opposed to the conventional monetary model. © 2014.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Since the collapse of the Bretton Woods fixed exchange rate system in 1971, much attention
has been paid towards finding a meaningful explanation of exchange rates. A wide range of
models have been proposed to understand movements in the exchange rate, one of which is
the monetary model (see Bilson, 1978; Frankel, 1979). Despite its rigorous theoretical
underpinnings by linking the nominal exchange rate to its monetary fundamentals (e.g.,
money, income, and interest rates), the resulting reduced form has had limited empirical
success until now. For example, although MacDonald and Taylor (1994) provided evidence of
a long-run relation between monetary fundamentals and nominal exchange rates, the signs
and magnitudes of estimated coefficients did not support the related monetary theories.
Groen (2000), and Mark and Sul (2001) among others also found some evidence in a panel
context, but this was under the assumption of a high order of heterogeneity across the
country models. Similarly, Rapach and Wohar (2002) found some support for the theory using
long time series, but this was related to different exchange rates and macro regimes, with
some evolution in the composition of products in price indices. Taylor and Peel (2000)
applied nonlinear methods to model a nominal exchange rate and monetary fundamentals
(relative money supply and relative income), but such results are often sensitive to a
small number of observations and become less robust as the sample evolves. Frömmel et al.
(2005) estimated the real interest differential (RID) model of Frankel (1979) applying the
Markov switching approach. However, the model was shown to relate to only one regime.
Furthermore, the empirical failure of this model has been specifically found in regard of
the US dollar–Japanese yen exchange rate. The evolution of this exchange rate has been
much debated over the recent years with no consensus over the factors that drive the
dynamics. For instance, Caporale and Pittis (2001) were unable to find a stable relation
based on a monetary model of this exchange rate. Chinn and Moore (2011) also failed to
find a long-run relation between the nominal dollar–yen exchange rate and its monetary
fundamentals (money, industrial production, and interest rate differentials) even when
they included cumulative order flow as opposed to the dollar–euro exchange rate. By
contrast, MacDonald and Nagayasu (1998) only found that a simplified version of the RID
model of Frankel (1979), that excluded the money demand functions, held for the yen–dollar
exchange rate for the period 1975:Q3–1994:Q3. Tellingly, in a recent paper, Obstfeld
(2009, p.1) comments that ‘the determinants of the yen's short- and even longer-term
movements remain mysterious in light of the development of Japan's macro economy’. A
possible explanation for the empirical failure of the dollar–yen exchange rate monetary
model is perhaps the breakdown of its underlying building blocks; that is, stable money
demand and purchasing power parity (PPP). Indeed, Hendry and Ericsson (1991) found that
the conventional money demand equation for the US was not stable. Whereas, Friedman (1988)
and McCornac (1991) confirmed the need for real stock prices to stabilise money demand
equations using data from the United States and Japan, respectively.1 Sarno and Taylor
(2002), on the other hand, found little support for the conventional notion of PPP by
surveying a range of empirical studies. This corresponds well with the classic findings of
Balassa (1964) and Samuelson (1964), which indicate that persistent deviations from PPP
arise from productivity differentials. Chinn (1997, 2000), and Wang and Dunne (2003) among
others showed that fluctuations in the nominal and real dollar–yen exchange rate are due
to the impact of differentials in productivity and government expenditure along with real
oil prices. This paper contributes to the existing literature by proposing a hybrid
monetary model of the dollar–yen exchange rate that takes into account the breakdown of
the aforementioned building blocks. That is, the proposed model captures both the monetary
and the real aspects of the economy, thereby circumventing some of the potential pitfalls
associated with earlier studies. More specifically, we examine the empirical performance
of the standard RID model, developed by Frankel (1979), against this proposed hybrid
version by employing the Johansen (1995) methodology and quarterly data from 1980:01 to
2009:04, a period characterised by high international capital mobility and volatility. The
RID model has been widely used as it combines aspects of the sticky-price approach with
the flexible-price one. Furthermore, this variant of the monetary approach is chosen
because it is a realistic description when variation in the inflation differential is
moderate as is the case between the US and Japan over the period under examination.2
Particularly, the theory underlines the role of expectations in different inflationary
environments and the associated rapid adjustment in capital markets. The hybrid version,
by contrast, is devised by using domestic and foreign money demand equations based on
broader asset classes and also accounting for the factors that cause PPP to fail. That is,
we incorporate real stock prices in the money demand equations,3 while we use the
productivity differential, relative government spending, and real oil price to explain the
persistence in the real dollar–yen exchange rate. The paper is organised as follows.
Section 2 provides the theoretical framework for the exchange rate monetary model; Section
3 outlines the econometric technique used and describes the data; Section 4 explains the
empirical results and the analysis; and finally Section 5 concludes.

<h>THEORETICAL FRAMEWORK</h>
---------------------

The monetary model of the exchange rate is based on the assumptions that money demand
equations are stable and that PPP holds. In this paper, we consider two forms of this
model and place them under econometric scrutiny. The first is the RID model developed by
Frankel (1979) and the second is a hybrid monetary model, proposed herein, that takes into
account factors affecting the stability of the respective money demand equations and the
validity of PPP. Otherwise, the RID model related to Eq. (8) hypothesises that an increase
in the domestic money supply relative to the counterpart foreign one increases domestic
prices and thus causes a one for one depreciation in the exchange rate (β1 = 1). An
increase in domestic income or a decline in the expected rate of domestic inflation
(proxied by the long-term interest rate) relative to the foreign one raises the demand for
money and thus causes an appreciation in the exchange rate (β2 < 0, β4 > 0). An increase
in the domestic nominal interest rate relative to the foreign one induces capital inflows
towards the domestic economy and thus causes an appreciation in the exchange rate (β3 <
0). For further details the reader is directed to Frankel (1979). However, Friedman (1988)
and subsequently McCornac (1991) and Caruso (2001) among others showed that the stability
of the money demand functions used to specify the monetary model, Eqs. (3) and (4),
depends on the inclusion of real stock prices. Furthermore, as Chortareas and Kapetanios
(2004) pointed out, there is limited support for the conventional notion of PPP for Japan.
Indeed, by visual inspection of Fig. 1, we find that the real dollar–yen exchange rate,
calculated as the nominal exchange rate adjusted for the domestic and foreign price levels
(see Eq. (6a) in Appendix A), does not appear to revert to mean. Balassa (1964) and
Samuelson (1964) attributed the inadequacy of PPP to real economic shocks, in particular,
to the unanticipated movement found in the productivity differentials between the traded
and non-traded goods sectors across the economies. Financial variables also appear
sensitive to the demand shocks associated with government expenditure (Chinn, 2000) and
the supply shocks related to real oil prices (Amano and van Norden, 1998). In the context
of the yen–dollar exchange rate, Chinn (1997, 2000), and Wang and Dunne (2003) found that
real economic factors were responsible for any persistence in the real yen–dollar exchange
rate during the post-Bretton Woods period. In addition to the coefficient restrictions
discussed earlier (β1 = 1, β2 < 0, β3 < 0, β4 > 0), the HM model suggests that the sign of
the coefficient on real stock prices, β5, depends on the extent to which the substitution
effect (positive) dominates the wealth effect (negative) in the money demand equation.
Based on the derivation provided in Appendix A, the sign of the coefficient on the
productivity differential depends on the relative competitiveness of the traded goods
sector. Specifically, an increase in the productivity of the traded sector relative to the
non-traded sector in the domestic economy compared to the foreign one results in a fall in
the domestic traded sector's goods prices relative to the foreign counterpart, and then an
exchange rate appreciation (β6 < 0). The differential in government expenditure captures
differences in demand side shocks (Chinn, 2000). As government expenditure is anticipated
to be spent largely on non-tradable goods such as services, an increase in domestic
government spending relative to the foreign counterpart should then increase the relative
price of domestic non-tradable goods, leading to an exchange rate appreciation (β7 < 0).
The sign of the coefficient on the real oil price is expected to be negative (β8 < 0)
because oil price is given in the US dollar and higher real oil price should lead to an
appreciation in the dollar (see Amano and van Norden, 1998). That is, the input costs in
Japan are highly sensitive to the oil price because Japan is a net importer country and
the third largest oil consumer and importer country after the United States and China.4

<hs>  The econometric approach</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~

The results associated with the Johansen test are well-defined when the VAR model is well-
specified (Johansen, 1995). The most appropriate lag length for the model is often
selected on the basis of information criteria such as the Schwarz Bayesian information
criterion (SBIC), the Akaike information criterion (AIC), and the Hannan–Quinn information
criterion (HQIC). However, Burke and Hunter (2007) suggest that there can be substantial
size distortion of the trace test relative to the null distribution when the selected lag
order is sub-optimal.5 Therefore, we extend the model to include adequate lags to remove
any serial correlation in case the lag selected based on information criteria does not
capture the dynamics. As a result of sharp changes as well as differences in monetary
policy between the United States and Japan throughout the sample period, we also include
impulse dummies that remove the impact of extreme observations relating to 1980:4, 1982:3,
2002:2, and 2008:4. The corresponding known events for the first two dummies relate to the
large short-term interest rate fluctuations in the United States and Japan in the late
1970s and early 1980s. Note that the fourth quarter of 1980 also corresponds with the end
point of the fiscally liberal 60s and 70s that led to the election of Ronald Reagan as the
US President and the Volker reforms at the Federal Reserve. The third dummy corresponds to
the monetary expansions (now termed quantitative easing (QE)) adopted by the Bank of Japan
from March 2001 to March 2003, while the fourth is due to QE in the United States as a
result of the 2007–2008 banking crisis. We suggest that by investigating these two
variable sets, we might be able to determine the key factors that identify the long-run
monetary model of the dollar–yen exchange rate and explain the short-run behaviour of the
different systems. Using series that are I(1), we can observe an exchange rate equation
based on the model in question by finding a cointegrating relation and showing via a
likelihood ratio test that this variable is neither long-run excluded (Juselius, 1995),
nor weakly exogenous (Johansen, 1992).6

<hs>  Data</hs>
  ~~~~

For this paper, we use quarterly seasonally unadjusted data, where available, for the
United States vis-à-vis Japan over the period 1980:1–2009:4. We choose the start of the
sample period in order to control for structural change in the Japanese financial system
because by the end of 1979, the interbank rates in Japan were deregulated, capital
controls were removed, and the certificate of deposit market developed (McCornac, 1991).
We use quarterly data as GDP data are not available on a monthly basis. The short-term
interest rates are represented by the official discount rates,7 whereas the long-term
interest rates are represented by the 10-year government bond yields. Moreover, we use the
consumer price index (CPI) to deflate the stock price indices represented by the S&P 500
in the United States and the Nikkei 225 in Japan. While government spending is defined as
government consumption in proportion to GDP, the productivity is defined as industrial
production divided by the corresponding employment level. The real oil price is the West
Texas Intermediate (WTI) Cushing crude oil spot price (in dollars per barrel) deflated by
the US CPI. The exchange rate (denoted as dollars per unit of yen), interest rates,
national income, industrial production, and price levels (CPI) are sourced from the IMF's
International Financial Statistics (IFS). Nonetheless, money supply (M1), oil price, and
stock prices are from Thomson DataStream.8 Government spending and employment figures, on
the other hand, are obtained from the OECD main economic indicators (MEI).

<h>EMPIRICAL RESULTS</h>
-----------------

A prerequisite for conducting cointegration tests is to check the time series properties
of the variables under investigation as to their order of integration. The null of non-
stationarity is tested using augmented Dicky–Fuller (ADF) tests (Dickey and Fuller, 1981)
and DF-GLS tests of Elliott et al. (1996). The results, as displayed in Tables 1 and 2,
indicate that all the variables require first differencing to be stationary, hence they
are integrated of order one (I(1)).9 Cointegration is then tested using the Johansen
(1995) procedure. The first subsection presents the analysis of the RID model; the second
subsection analyses the HM model; and finally validation of the hybrid model is reported
in the third subsection.

<hs>  Long-run analysis of the RID model</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

For the data set XRID,t, the SBIC, HQIC, and AIC indicate that the VAR is first order (p =
1). However, in order to remove any serial correlation and enhance the specification of
the model, we require p = 4. The Lagrange multiplier (LM) test for the presence of serial
correlation and ARCH along with the Jarque–Bera test of non-normality is reported in Table
3 and suggests that, at the 5% level, there is no evidence of misspecification for the
model. On the basis of this specification, the estimated eigenvalues and trace statistics
are reported in Table 4. By inspection of the above results the estimated coefficient on
the relative money supply has the sign expected by theory, even though it is large
relative to the hypothesised magnitude of 1. Moreover, based on one-sided inference, we
consider it significant at the 5% level. However, the coefficients on the rest of the
monetary fundamentals have signs that are not consistent with the theory, although
relative income and the long-term interest rate differential are highly significant (at
the 1% level). To provide further insights into this long-run relation, we conduct long-
run exclusion (LE), weak exogeneity (WE), and stationarity tests by imposing restrictions
on α and β (see Johansen, 1995); the latter tests are conducted to provide further
evidence with regard to the stochastic properties of the series. Even though it is often
felt that the normalisation is innocuous, the significance of the LE test is informative
of the likely appropriateness of a normalisation. According to Boswijk (1996), empirical
identification generally requires satisfaction of further rank conditions. However, Burke
and Hunter (2005; chapter 5) argue that any coherent strategy for identification ought to
preclude normalisation on variables that are either long-run excluded or weakly exogenous.
Cointegration is a property of two or more non-stationary series and thus normalisation is
also inappropriate on stationary variables. The tests of LE, WE, and stationarity are
asymptotically distributed chi-squared (Johansen, 1992) and in Table 5 we report our
results on a variable by variable basis. The LE tests are conducted by imposing a zero
restriction on the relevant elements of β. If a zero restriction on an element of β for a
specific variable is not rejected, then the long-run relation cannot be normalised on this
variable. The WE tests, by contrast, are carried out by imposing a zero restriction on
elements of α in turn. If a zero restriction on an element of α for a particular variable
is not rejected, then this variable can be considered weakly exogenous; it drives the
system instead of adjusting to it. The stationarity tests are conducted, under the null
hypothesis of stationarity, in the multivariate setting by fixing each element in turn in
a single cointegrating vector to unity and the remaining elements to zero. As is evident
from Table 5, the LE tests indicate that, except for the relative income and long-term
interest rate differential, all the other variables can be excluded from the cointegrating
relation. Hence, any long-run model based on the exchange rate may be ill defined, as the
related parameter cannot be distinguished from zero. In the subsequent panel, the
proposition that the exchange rate and short-term interest rate differential are weakly
exogenous also cannot be rejected. This implies that, at best, the long-run relation ought
to be conditioned on the exchange rate instead of being normalised on. Hunter (1992) among
others presents similar findings for the exchange rate. In conclusion, despite the
existence of a long-run relation among the variables of the RID model, such a relation
cannot explain the behaviour of the exchange rate as this variable can be both excluded
and viewed as weakly exogenous for the cointegrating vector. However, the tests of
stationarity following from the restriction mentioned before on the VAR support the
proposition that the series are all difference stationary (see Table 5), in line with the
results of single unit root tests in Tables 1 and 2.

<hs>  Long-run analysis of the HM model</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The findings given above cast serious doubt on the conventional monetary model regarding
the dollar–yen exchange rate. Therefore, we consider it of paramount interest to
investigate the reasons for this failure. To this end, the VAR model is now based on the
vector XHM that represents the hybrid version. Since the price of oil is a global factor
and all other factors are differentials between the United States and Japanese variables,
we treat the real oil price as exogenous to the system.10 Indeed, the test suggests a non-
rejection of the null hypothesis of weak exogeneity with a p-value of 0.741. This finding
is also consistent with the intuition of Amano and van Norden (1998) that oil prices in
the decades preceding their study were governed by the major supply-side shocks resulting
from political instability in the Middle East, and are thus external to the developed
economies. With regard to the VAR specification, the SBIC, HQIC and AIC suggest a lag
length p = 1, while diagnostic tests imply that p = 3 is required to improve the
specification. The reported diagnostics in Table 6 suggest that, at the 5% level, the
model does not suffer from serial correlation using the LM test up to order 8, and the
same applies for ARCH effects up to order 8. However, the multivariate normality test is
rejected, where the sources of such failure seem to result from excess kurtosis in the
money supply and productivity differentials. Since Gonzalo (1994) demonstrated a lack of
sensitivity of the cointegrating rank to excess kurtosis, we conclude that these findings
are robust. Accordingly, Table 7 reports the trace test related to the HM model. It is
evident that the null hypothesis of no cointegration is rejected, but evidence for more
than one cointegrating vector cannot be rejected at the 5% level. Since the cointegrating
rank does not change by the inclusion of the augmenting factors, this indicates that these
factors follow stochastic trends common to the nominal exchange rate and its monetary
fundamentals in the RID model. Long-run exclusion tests are likely to give more
information regarding the nature of the contribution of the augmenting factors and also
the variables on which the long-run relation may be normalised. Hence, Table 8 reports the
LE, WE, and stationarity tests of the variables included in the HM model. The stationarity
tests imply that none of the variables in the cointegrating relation is stationary,
consistent with the results reported in Tables 1 and 2. The LE tests, by contrast,
indicate that the real oil price is the primary candidate for exclusion in the long-run
relation, while the money supply and real stock price differentials could be excluded on a
single-variable basis, although this would be rejected at the 15% level. However, at this
stage, we do not exclude any variable based on a single-variable test. In the next
subsection, we use these results to obtain a more parsimonious long-run relation. Our key
findings are that the long-run exclusion of the nominal exchange rate is rejected now, and
that the exchange rate appears not to be weakly exogenous for the HM model (see panel B in
Table 8). The change in WE status is a de facto indication of changes in long-run feedback
and is of paramount interest (Juselius and Macdonald, 2004). Unlike the RID model, this
finding indicates that the nominal exchange rate in the HM model adjusts to the long-run
equilibrium. That is, it does not force the system when such a system accounts for the
relative real stock prices, the productivity differential, relative government spending,
and the real oil price. In addition to the real oil price on which the system is
conditioned as stated earlier, the tests reported in Table 8 (panel B) also indicate that
we cannot reject the findings that relative money supply, relative income, short-term
interest rate differential, relative real stock prices, productivity differential, and
relative government spending are weakly exogenous at the 5% level for the long-run
relation, although the long-term interest rate differential is not. As shown from Eq.
(13), the estimated coefficients on monetary fundamentals (relative money supply, relative
income, and short-term and long-term interest rate differentials) are all significant and
consistent with monetary theory. More specifically, the coefficient on the relative money
supply is not materially different from 1, and is significant based on a one-sided test at
the 5% level. All the other monetary variable coefficients (relative income and short-term
and long-term interest rate differentials) have their hypothesised signs and are
significant at the 1% level. Furthermore, as hypothesised by Frankel (1979), the parameter
on the long-term interest rate differential is greater than that on the short-term
interest rate differential in absolute value. Except for the real oil price, all the
factors that have been used to augment the monetary model have significant parameters.
This implies that the real oil price can be excluded from the long-run relation and, as
with Johansen and Juselius (1992), treated as strictly exogenous. Consistent with Friedman
(1988) and Caruso (2001), the coefficient on the relative real stock price is negative
implying that the wealth effect dominates the substitution effect in the underlying money
demand functions for the United States and Japan. The coefficients on the productivity
differential across the industrial sectors and relative government spending are negative
and significant. This suggests that higher domestic productivity or government spending
compared to their foreign counterpart results in an exchange rate appreciation. The fact
that the real oil price can be excluded from the long-run part of the VAR system suggests
that it affects the long-run only indirectly by enhancing the econometric performance of
the model.

<hs>  Hybrid model validation</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

The above results strongly indicate that the HM model dominates the RID model on
theoretical and econometric grounds in explaining the dollar–yen exchange rate in the
long-run. However, to check the robustness of our results, we conduct two further
analyses. First, we use the results on LE and WE to obtain a more specific and robust
formulation of the long-run relation based on the HM model. A similar approach has also
been used by MacDonald and Nagayasu (1998), though they examine a simplified version of
the RID model of the yen–dollar exchange rate excluding money demand functions. Next, we
sequentially impose zero restrictions on the loading factors, α, of the standard monetary
fundamentals related to relative money supply, relative income, and short-term interest
rate differential. These weak exogeneity restrictions are empirically plausible given the
size of the adjustment coefficients and also consistent with monetary theory. The tests,
as displayed in Table 9, indicate that the imposed restrictions cannot be rejected.
Moreover, the constrained final long-run relation normalised on the exchange rate suggests
the significance of monetary variables with their hypothesised signs, as found in the
previous subsection. The trace test also implies that there is still a single
cointegrating vector among the variables (these results are unreported). Overall, this
demonstrates the robustness of our results in terms of the long-run formulation and direct
impact of the augmenting factors on the long-run exchange rate monetary model.11 Then, we
subject our proposed HM model to an array of forward and backward recursive stability
tests proposed by Hansen and Johansen (1999) to gain further insights into its adequacy as
a long-run exchange rate model. The results reported here relate to the behaviour of the
max tests of β and are displayed in Fig. 2. The forward and backward tests appear
respectively in the Figure's left and right panels, with the corresponding 5% critical
value represented by the solid line. Note that in providing these stability tests, the
short-run effects (X(t)) compared to those of the long-run R1(t) are concentrated out. In
a broad sense, the model shows a reasonable degree of stability of the parameters in the
cointegrating vector. Hence, the model seems to be adequate and does not exhibit
structural breaks in relation to the long-run for the period under observation.

<h>CONCLUSIONS</h>
-----------

In this paper, we re-examine the dollar–yen exchange rate using two versions of the
monetary model. The first is the conventional real interest differential (RID) model of
Frankel (1979) and the second is a hybrid monetary (HM) model, proposed herein, that
incorporates on the one hand real stock prices to capture the stability of money demand
and on the other, the productivity differential, relative government spending, and the
real oil price to explain the persistence in the real exchange rate. Both models are
estimated using the Johansen cointegration methodology and quarterly data from 1980 to
2009, a period characterised by high international capital mobility, as well as periodic
volatility in the dollar–yen exchange rate. Although a single cointegrating vector exists
for both models, the long-run exclusion and weak exogeneity tests inform us that the HM
version gives an appropriate long-run explanation of the monetary model of the dollar–yen
exchange rate. The enhanced performance of the HM model derives from the following
considerations to the conventional monetary model. First, the stability of money demand
relations is taken into account by the inclusion of key variables that impact on
transactions (Friedman, 1988). A key feature of globalised financial markets is a highly
active market in cross-border investments, mergers and acquisitions, and cross-listed
stocks. In particular, the futures contract on the Nikkei is listed as an asset in the US
stock market. Second, the persistence of the real exchange rate, which reflects primarily
the impact of the non-traded goods, is taken into consideration by accounting for
productivity and government expenditure differences. In essence, these differences may be
due to the relatively insular nature of Japanese society limiting the effectiveness of
arbitrage. The literature also suggests that the real oil price affects such persistence,
but the empirical findings herein show an indirect impact of such a price via the dynamic
specification of the VAR model. Contrary to the conventional monetary model, the results
also suggest that the dollar–yen exchange rate in the hybrid model is driven by money,
income, and short-term interest rate differentials, but not the reverse. This implies a
substantial role for real economic and financial market variables in a well-formulated
monetary model for the determination of the long-run exchange rate.


<h>REFERENCES</h>
----------

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<ART>Non-reservation price equilibria and consumer search
====================================================

Authors: Maarten C.W. Janssen, Alexei Parakhonyak, Anastasia Parakhonyak
DOI: 10.1016/j.jet.2017.08.003
Year: 2017  |  Pages: 120-162
ASJC codes: 2002
Keywords: Asymmetric information, Consumer learning, Non-reservation price equilibria, Sequential search

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Reservation price equilibria (RPE) do not accurately assess market power in consumer search markets. In most search markets, consumers do not know important elements of the environment in which they search (such as, for example, firms' cost). We argue that when consumers learn when searching, RPE suffer from theoretical issues, such as non-existence and critical dependence on specific out-of-equilibrium beliefs. We characterize equilibria where consumers rationally choose search strategies that are not characterized by a reservation price. Non-RPE always exist and do not depend on specific out-of-equilibrium beliefs. Non-RPE have active consumer search and are consistent with recent empirical findings.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

In consumer search markets, firms have market power due to the fact that some consumers do
not make price comparisons. Firms take this market power into account when deciding on
price. This paper addresses the question of whether, by focusing on consumers following
reservation price strategies, the existing consumer search literature accurately evaluates
this market power due to search frictions. A reservation price strategy is a cut-off
strategy: after observing a price at or below some critical value, consumers decide to
buy, otherwise they continue to search. In markets where there is uncertainty about the
underlying factors determining firms' pricing behavior, there are important theoretical
reasons to consider other search strategies than reservation price strategies. Rothschild
(1974) drew attention to the fact that when consumers do not know from which distribution
of offers they obtain their information, the optimal consumer search rule may well be
different from the typical reservation price rule.1 The main reason is that on the basis
of past search observations, consumers learn about the environment in which they search.
Depending on the environment, it may well be that, after observing a relatively good
outcome, consumers infer that even better outcomes are likely to be observed in the next
search round and rationally conclude to continue to search, whereas, after observing a
relatively bad outcome, consumers infer that better outcomes are unlikely and thus stop
searching. The consumer search literature has, by and large, neglected this observation.
The celebrated models by Stahl (1989) and Wolinsky (1986), and much of the literature that
takes these models as a starting point, study environments without underlying uncertainty
and in such theoretical environments the optimal search rule is indeed a reservation price
rule. In consumer search markets where consumers are uninformed about firms' underlying
costs (and this probably comprises most markets where consumer search is important),
learning is an important part of the search process. There are some papers on learning and
consumer search that take consumer uncertainty about firms' costs into consideration (see,
Benabou and Gertner, 1993; Dana, 1994; Fishman, 1996 and more recently, Yang and Ye, 2008;
Tappata, 2009; Janssen et al., 2011 and Chandra and Tappata, 2011). The observations by
Rothschild (1974) are of immediate concern to these environments, but the relevant
economics literature has continued to focus on equilibria where the consumer search rule
is characterized by a reservation price. Some of this literature is inspired by retail
gasoline markets where the common wholesale price of crude oil is the most important
determinant of the (variation in) costs of retailers, and consumers are uncertain about
these costs due to the large fluctuations of this wholesale price on the world market.
Although our focus in this paper is on consumer search in retail markets, the issues we
address are also relevant for other markets. For example, Benabou and Gertner (1993) is
motivated by macroeconomic concerns about inflationary uncertainty and the consequences
for firms' mark-ups, while a recent paper by Duffie et al. (2017) considers over-the-
counter (OTC) financial markets and the role of benchmarks in these markets. The current
paper is also relevant for the labor search literature where workers search for a better
wage. In labor markets, it is natural that the wage distribution depends on the business
cycle and that firms are better informed about the business cycle than workers. In that
case, workers learn about the wage distribution while searching for another job and their
search behavior does not need to follow a reservation wage strategy. In all these markets,
there is uncertainty and asymmetric information about a common component that determines
the distribution of offers and one needs to understand how the uninformed side (consumers,
workers) search and simultaneously learn in such an environment. Our paper is the first to
systematically incorporate Rothschild's observations on non-reservation price strategies
into an equilibrium search model with endogenous firm behavior.2,3 Benabou and Gertner
(1993) also mention the fact that in their model reservation price equilibria (RPE) may
not exist. They set up the equations that have to be satisfied in a non-RPE. They perform
some numerical analysis for some parameter values, but they neither have an analysis
characterizing these non-RPE, nor do they show the conditions under which these equilibria
exist.4 The literature studying RPE in environments where consumers are uninformed about
firms' cost is unsatisfactory for a number of reasons. First, RPE are known to exist only
if the search cost is relatively large and/or the uncertainty about costs is relatively
small (cf., Dana, 1994 and Janssen et al., 2011). It is unclear what type of equilibria do
exist for small search cost or large uncertainty about common costs. Second, RPE
implicitly assume certain out-of-equilibrium beliefs and it is unknown whether these out-
of-equilibrium beliefs satisfy game theoretic refinement concepts commonly employed in
asymmetric information games. Third, one would expect that when costs are uncertain
consumers may engage in active costly search in equilibrium. When consumers observe a high
price, they are uncertain about whether this is due to a relatively high (common)
production costs or whether this particular firm is charging a high margin. RPE in these
homogeneous goods markets have firms charging prices below the consumer reservation price,
however, and therefore all consumers buy at the first firm they visit. This lack of
consumer search gives firms substantial market power, but it may well be that RPE
overestimate the true market power because they underestimate consumers' search intensity.
In response to these points, this paper first sharpens existing results on RPE. We show
(i) that independent of out-of-equilibrium beliefs, RPE do not exist when the uncertainty
about production cost is relatively large and (ii) that an RPE, even if it exists, is
sensitive to the specification of out-of-equilibrium beliefs and do not satisfy, for
example, the logic of the D1 equilibrium refinement (hereafter the D1 logic, see Cho and
Sobel, 1990). If the uncertainty about cost is relatively large, any equilibrium should
have active search. We then continue to characterize non-RPE and show that they exist for
all parameter values and that there are parameter values for which multiple non-RPE exist.
Thus, non-RPE resolve the non-existence problem that RPE suffer from. Moreover, in any
non-RPE, consumers actively search beyond the first firm. In particular, there is a region
of “high” prices that are set with positive probability such that consumers are
indifferent between buying and searching and consumers continue to search with strictly
positive probability. When the cost uncertainty is large, market prices may be
substantially below the market prices predicted by RPE due to active search by consumers.
On the other hand, when cost uncertainty is small, expected market prices are larger in
non-RPE. Thus, whether or not RPE overestimate the market power of firms depends on the
uncertainty about cost. In a recent empirical paper, De los Santos et al. (2012) show
that, when buying books online consumers do not follow reservation price strategies. These
strategies predict that (i) consumers buy from the last store visited unless all stores
have been visited and (ii) the decision whether to continue to search depends on the
outcome of the previous search with consumers observing lower prices deciding to buy, and
consumers observing larger prices deciding to continue searching. Their evidence
contradicts these predictions.5 In this paper, we show that their empirical findings are
consistent with equilibrium behavior under non-reservation price strategies, as follows.
When the cost uncertainty is relatively large, non-RPE have a region of intermediate
prices where the probability of a sale is lower when the price is low. At lower prices,
consumers rationally expect to get lower prices on the next search round and this may
induce them to search more. In particular, we show that consumers may accept higher prices
in the first search round, while rejecting lower prices. In an extension to oligopolistic
markets, we also show that the optimal sequential search behavior of consumers is
consistent with consumers going back to previously sampled firms, before they have sampled
all firms.6 There is also a relationship with the marketing oriented literature on
reference price effects (see, e.g., Putler, 1992; Kalyanaram and Winer, 1995 and Mazumdar
et al., 2005). This literature points to the fact that consumers have particular pricing
points around which consumer demand is very sensitive to price changes. This may lead to
situations where consumer demand drops significantly if firms price above this reference
point, whereas at higher prices, consumers are willing to buy again. Such “reference
point” demand behavior can occur in non-RPE when the cost uncertainty is large. After
observing intermediate prices above the “reference price”, consumers rationally infer that
these prices are not chosen by high cost firms. Knowing costs are low, consumers find
these prices too high to buy, however, and they continue to search for sure. This
inference creates a gap in the equilibrium price distribution of the low cost firms. The
rest of the paper is organized as follows. Section 2 describes the model and the
equilibrium concept. Section 3 discusses how RPE depend on assumptions regarding out-of-
equilibrium beliefs and why (regardless of these out-of-equilibrium beliefs) they do not
exist when cost uncertainty is relatively large. Section 4 describes our analytical
results on non-RPE. Section 5 shows, by means of a numerical analysis, the effects of cost
uncertainty on profits, expected prices and consumer welfare. Section 6 briefly discusses
a generalization of our model to the case of imperfectly correlated production costs and
oligopoly markets with N firms. We show that with three or more firms, the optimal search
rule may imply that consumers first continue searching another firm, and then go back to a
previously sampled firm before all firms are sampled. Section 7 concludes with a
discussion, while proofs are given in two Appendices.

<h>THE MODEL AND EQUILIBRIUM CONCEPT</h>
---------------------------------

The timing of the model is as follows. First, Nature chooses c for both firms. After
observing c, firms simultaneously decide on their prices. Finally, consumers search and
make their purchase decisions. It is by now a standard argument in the search literature
with symmetric information that due to the presence of shoppers and non-shoppers there do
not exist equilibria with mass points in the price distributions. This argument continues
to hold in our model with asymmetric information as far as pure pricing strategies are
concerned: even if all non-shoppers continue to search, an undercutting firm will sell to
all shoppers and non-shoppers that first visit that firm. In the present model, this
argument does not extend, however, to ruling out pricing distribution with mass points.
Given that equilibria have to be in mixed strategies and that we prove that equilibria
without mass points always exist, we restrict our attention to mixed pricing strategies
without atoms. As explained in the Introduction, the existing literature focuses on
reservation price equilibria, which are defined as follows. When investigating non-RPE, we
focus on equilibria satisfying the logic of the D1 criterion (Cho and Sobel, 1990).10 The
D1 criterion was developed in the context of pure signaling games with one sender. Our
model is a two-sender game, where the beliefs of the receivers (the non-shoppers) are only
based on the single price they have observed. As firms are of the same type, the out-of-
equilibrium belief of non-shoppers is simply a mapping from the observed price to the type
distribution of cost, as in the one-sender game. Thus, from the set of equilibria that do
not satisfy Definition 1, we focus on those equilibria that satisfy the D1 logic and that
are sufficiently smooth. For easy reference, we refer to such equilibria in the rest of
the paper as non-reservation price equilibria (non-RPE). There may exist other equilibria
that do not satisfy the properties of a RPE and that do not satisfy the D1 requirement and
are not smooth. We do not consider these equilibria in our paper as we show that even with
the additional requirements of D1 and smoothness, we can guarantee existence. Moreover,
the equilibria we consider are interesting in their own right and do not depend on
arbitrary out-of-equilibrium beliefs or on more technical issues related to non-
smoothness.

<h>RESERVATION PRICE EQUILIBRIA</h>
----------------------------

In this Section, we summarize some existing results on RPE, (i) prove that they do not
exist if the cost uncertainty is large and (ii) prove that they do not satisfy the D1
logic even if they do exist. We next show that if an RPE does not exist, any equilibrium
without mass points should have a region of prices where non-shoppers actively search
(search with positive probability). There are two important corollaries, which follow
immediately from Proposition 3. First, as in any RPE firms' pricing distributions are
atomless (see, e.g. Stahl, 1989), and there is no active search (see Dana, 1994), we
immediately have the following corollary. All reservation price equilibria do not satisfy
the D1 logic. Second, by Definition 2 we have In any non-reservation price equilibrium
non-shoppers search with positive probability.

<h>CHARACTERIZATION AND EXISTENCE OF NON-RPE</h>
-----------------------------------------

The proof is constructive and consists of several Lemmas. It is formally developed in
Appendix B. For a range of parameter values the equilibrium is not unique, while for other
parameter values it is unique. We now extensively describe how for any set of parameter
values we construct an equilibrium. We end this Section discussing how our analysis may
shed some light on the empirical observations we mentioned at the end of the Introduction.
Numerically, one can compare for a given cost realization (i) the expected first price
observation conditional on the price being accepted and (ii) the expected first price
observation conditional on it not being accepted. De los Santos et al. (2012) observe that
in their sample the first conditional expected price is larger than the second, and they
rightly claim that this is inconsistent with RPE. For the parameter values used in Figs.
3–5, one can compute and compare both conditional expected prices to conclude that for the
high cost realization these non-RPE are consistent with the findings of De los Santos et
al. (2012): for Fig. 4 the respective numbers are 42.94 and 42.83, for Fig. 3 the numbers
are 50.81 and 49.83, while for Fig. 5 they are 45.19 and 45.11, respectively. Thus, we
conclude that the observations of De los Santos et al. (2012) are not necessarily
inconsistent with sequential search, although they are inconsistent with reservation price
strategies. Finally, equilibria where the low cost price distribution has a non-convex
support may be interpreted as a search theoretic foundation for the reference price
principle that is discussed in marketing (see the references in the Introduction). In our
model, reference prices endogenously arise from the fact that consumers rationally infer
that a certain low price will only be set when cost is low, and if the common cost is
really low, then the chances of finding low prices are so high that it is rational to
continue searching for better deals. Thus, it is better for firms not to set prices just
above these reference prices.

<h>COMPARATIVE STATICS AND COMPARING MODELS</h>
----------------------------------------

We are now in a position to compare the equilibrium outcomes of our model with two
benchmark models, and to perform some numerical comparative statics analysis. On one hand,
we use Stahl (1989) as a benchmark to show the implications of cost uncertainty. On the
other hand, we use Dana (1994), or equivalently Janssen et al. (2011), as a benchmark for
the outcome of RPE with cost uncertainty. As shown in Janssen et al. (2011), the expected
price under RPE is larger than the weighted average of the expected price of the high and
low cost equilibria as developed by Stahl (1989) and in that sense, consumers are worse
off under cost uncertainty. In this Section we show that this result may well be reversed
for non-RPE. The first two panels (8(a) and 8(b)) show the dependence on search cost. For
small search cost, a large fraction of non-shoppers performs two searches and the expected
price is close to the average marginal cost of 25. When the search cost increases from
initially low levels, the expected price increases and the fraction of non-shoppers
performing two searches decreases (giving firms more market power). At search cost levels
close to 2, there are multiple gap equilibria, and it may be that the expected price is
decreasing in search cost. When the search cost further increases, a no-gap equilibrium
emerges and the probability of non-shoppers searching twice becomes very close to 0. Panel
(8(b)) also shows that starting from an initially small search cost, non-shoppers will
search less when the search cost increases. In this way, non-shoppers partially mitigate
the increase in market power typically associated with higher search cost. The last two
panels (8(e) and 8(f)) show the dependence on the probability that the cost is high. When
this probability is high, there is a no-gap equilibrium and consumers search very little,
since there is a low probability of obtaining a substantially lower price. In this region
the higher the α, the higher the expected price. For lower values of α, there is a
monopolistic gap equilibrium with qualitatively similar properties. When α is sufficiently
low, there are multiple gap equilibria and the incentives to search can be high, pushing
the prices down. The expected price can be both increasing and decreasing in α depending
on which of the regular gap equilibria is chosen.

<h>EXTENSIONS</h>
----------

In this Section, we deal with two important extensions of our general analysis. The first
relates to introducing more general forms of correlation between firms' costs, the second
relates to a first analysis of oligopoly markets with sequential search.

<hs>  Introducing an idiosyncratic cost component</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In Appendix C, we describe the analysis for the case where there is no uncertainty
concerning the common cost component (the “pure idiosyncratic cost shock” case). The main
take away from that analysis is that (for the same common cost component) a firm with a
low idiosyncratic cost state randomizes prices over a support that is below and does not
overlap with the support of the price distribution of a firm with a high idiosyncratic
cost state. We conclude that it is entirely possible to extend the analysis in the main
body of the paper and deal with situations where firms' cost has a common and an
idiosyncratic component. Fig. 9 shows that if we add idiosyncratic cost uncertainty, the
expected market price can be both lower and higher than without this uncertainty. The
impact of idiosyncratic cost uncertainty on expected prices is very different than the
impact of common cost uncertainty, as there is no consumer learning. The main effect is
through the fact that the low and high cost distributions are not overlapping and that the
reservation price is based on a weighted average of the expected prices of these two
distributions.

<hs>  Oligopoly markets</hs>
  ~~~~~~~~~~~~~~~~~

It is not too difficult to reformulate our analysis to an oligopoly model by replacing
sequential search with “newspaper search” a la Salop and Stiglitz (1977) and Dana (1994).
Under newspaper search, a consumer pays a search cost only once to see all remaining
prices. Thus, in both the duopoly model with sequential search and the oligopoly model
with newspaper search, a consumer effectively has to take the decision whether or not to
continue to search only once.

<h>DISCUSSION AND CONCLUSION</h>
-------------------------

In this paper we have considered consumer search markets where firms' underlying common
cost is unknown to consumers. If consumers do not know the prices different firms charge,
it is natural that they also do not know the underlying cost. We have argued that in this
environment of cost uncertainty, the standard RPE considered in the consumer search
literature suffer from severe limitations. It was already known that RPE do not always
exist, but we add that RPE implicitly assume specific out-of-equilibrium beliefs that do
not satisfy standard game theoretic refinements. We characterize non-RPE that do not
depend on specific assumptions regarding out-of-equilibrium beliefs and show that these
equilibria always exist. Non-RPE may provide a significantly different assessment of the
market power firms derive from search frictions. In non-RPE, non-shoppers are indifferent
between buying and continuing to search over a range of prices. As prices in this range
are set with positive probability, these non-RPE have active search with positive
probability in equilibrium. Thus, we extend the Rothschild (1974) finding by showing in a
model with endogenous price setting that in equilibrium firms price in such a way that
consumers do not choose reservation price strategies. The fact that consumers rationally
search more with cost uncertainty in non-RPE explains why market power may be
overestimated in RPE. The additional search has a quantitatively important pro-competitive
effect on prices. Our results on non-RPE also have important consequences for the
empirical literature on consumer search models that has recently taken off. Non-RPE may
explain the observations of De los Santos et al. (2012) and Honka and Chintagunta (2017),
as in these equilibria (i) consumers may rationally continue to search at lower prices,
while they buy at higher prices and (ii) consumers may stop searching and buy at a
previously visited store, before they have observed all prices in the market (see our
oligopoly extension in Section 6). Moreover, the price distributions of non-RPE are quite
different from the regular price distributions found in RPE. It would be interesting to
see whether these price distributions provide a good fit with empirical data. As a first
inquiry into non-RPE, we have analyzed a stylized model limiting the immediate
applicability of this paper to real world markets.23 In extensions, we have shown that
some of the equilibria extend to oligopoly markets, and, importantly, we have dealt with
markets where firms' cost consists of an idiosyncratic and a common cost component.
Obviously, in an oligopoly framework one may want to consider a continuum of possible cost
states. Such an extension of the present paper would be important in environments where
the firms' cost is determined by an upstream firm (who can choose a continuum of different
price levels). In such an environment, Janssen and Shelegia (2015a) have characterized
interesting properties of RPE, but they also show such equilibria do not always exist.
Non-RPE would solve this non-existence issue and it is natural to inquire into the
qualitative properties of such equilibria. Bagwell and Lee (2014) provide such an analysis
for the case where cost has an idiosyncratic component only. An obvious next step is to
see whether our analysis on learning about a common cost component can be combined with
their analysis. One important issue that needs to be addressed in the generalizations to
oligopoly markets is how consumer inferences after observing two (or more) prices interact
with the consumer search decisions. In the oligopoly extension analyzed in this paper, we
dealt with the easiest of different possible cases that can arise. In general, however,
different possible search behaviors interact in a complicated way with the incentive of
firms to choose different prices. This paper made a first step analyzing non-RPE. There
are many theoretical and empirical challenges that lie ahead.


<h>REFERENCES</h>
----------

  [2] Roland Benabou, Robert Gertner. Search with learning from prices does increased inflationary uncertainty lead to higher markups. doi:10.2307/2297813
  [3] Ambarish Chandra, Mariano Tappata. Consumer search and dynamic price dispersion: An application to gasoline markets. doi:10.1111/j.1756-2171.2011.00150.x
  [5] In Koo Cho, Joel Sobel. Strategic stability and uniqueness in signaling games. doi:10.1016/0022-0531(90)90009-9
  [7] Babur De Los Santos, Ali Hortacsu, Matthijs R. Wildenbeest. Testing models of consumer search using data on web browsing and purchasing behavior. doi:10.1257/aer.102.6.2955
  [8] Darrell Duffie, Piotr Dworczak, Haoxiang Zhu. Benchmarks in Search Markets. doi:10.1111/jofi.12525
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  [10] Elisabeth Honka, Pradeep Chintagunta. Simultaneous or sequential? Search strategies in the U.S. auto insurance industry. doi:10.1287/mksc.2016.0995
  [11] Maarten Janssen, Sandro Shelegia. Consumer search and double marginalization. doi:10.1257/aer.20121317
  [12] Maarten Janssen, Paul Pichler, Simon Weidenholzer. Oligopolistic markets with sequential search and production cost uncertainty. doi:10.1111/j.1756-2171.2011.00144.x
  [14] Tridib Mazumdar, S. P. Raj, Indrajit Sinha. Reference price research: Review and propositions. doi:10.1509/jmkg.2005.69.4.84
  [17] Richard Rogerson, Robert Shimer, Randall Wright. Search-theoretic models of the labor market: A survey. doi:10.1257/002205105775362014
  [19] Steven Salop, Joseph Stiglitz. Bargains and ripoffs: A model of monopolistically competitive price dispersion. doi:10.2307/2296903
  [21] Mariano Tappata. Rockets and feathers: Understanding asymmetric pricing. doi:10.1111/j.1756-2171.2009.00084.x
  [22] Asher Wolinsky. True monopolistic competition as a result of imperfect information. doi:10.2307/1885694
  [23] Huanxing Yang, Lixin Ye. Search with learning: Understanding asymmetric price adjustments. doi:10.1111/j.0741-6261.2008.00027.x
<ART>On the cost of misperception: General results and behavioral applications
=========================================================================

Authors: Olivier Gossner, Jakub Steiner
DOI: 10.1016/j.jet.2018.08.003
Year: 2018  |  Pages: 816-847
ASJC codes: 2002
Keywords: Bounded rationality, Memory, Overconfidence, Perception bias

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

In a choice model, we characterize the loss induced by misperceptions of payoff-relevant parameters across a distribution of decision problems. When the agent cannot avoid misperceptions but has some control over the distribution of errors, we show that strategies that minimize loss from misperception exhibit systematic biases, akin to some documented in the behavioral and psychological literatures. We include illusion of control, order effect, overprecision, and overweighting of small probabilities as illustrative examples.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Within economic discourse, the idea that the human mind is imperfect and that some
information is necessarily lost during any decision process dates back at least to Simon
(1955). Under this premise, an agent faces, apart from the standard action choice, a
problem of error management. In economic decision making, some mistakes in perception of
payoff-relevant parameters are costlier than others, and this asymmetry has an impact on
the frequency of different types of perception errors. In this paper, we relate error
management to known observed behavioral biases. In order to understand the direction of
biases arising under second-best perception strategies, we need first to understand the
associated costs of under- or over-estimating payoff-relevant parameters. Our agent first
receives some statistical information on a state of nature which can be either high or
low, and this information translates into an objective belief p that the state is high. In
a choice stage, she recalls this information imperfectly and ends up with a subjective
belief q that the state is high. She then chooses an action that is optimal under her
subjective belief q within a fixed choice set. Due to belief distortion, her choice may
differ from the optimal one. We ask how large is the payoff loss incurred from the
misperception of p for q. Equipped with this loss characterization, we study a class of
error-management problems in which the agent chooses a distribution of perception errors
that performs well across all decision problems that she encounters in her environment. We
follow principles from the ecological rationality literature, in that our agent is unable
to reoptimize the perception strategy in each encountered decision problem separately but,
instead, must choose a perception heuristic that fits her environment.1 One feasible
perception strategy is to memorize the true probability value. Under such a strategy, the
recalled probability is in expectation equal to the true one. It turns out, however, that
this unbiased perception strategy is generically suboptimal, and the agent benefits from
memorizing m distinct from the true probability p. A misperception of q instead of p
causes a loss only when the optimal choices at p and q differ. This happens precisely when
there exists a probability s between p and q such that the agent is indifferent at s
between the two lotteries. The likelihood that such a tie arises at s depends on s in an
intuitive way. Since the expected value of each lottery is a convex combination of the two
standard normal draws, its variance is lower the closer s is to 1/2. Thus, the likelihood
of a tie at probability s is a single-peaked function of s attaining its maximum at 1/2.
This implies that misperceptions of p for a value q towards the direction of 1/2 are more
likely to distort choices than misperceptions in the opposite direction: undervaluation of
one's own ability to predict the binary state leads to suboptimal choice more often than
the symmetric opposite error. Since the agent can shift the distribution of her perception
error by controlling the memorized probability value, it is optimal for her to memorize a
value further away from 1/2 than the truth, hence to exhibit an overprecision bias. Apart
from the overprecision application, we illustrate our methodology in three additional
examples: illusion of control, order effect, and probability weighting. In each
application, we make natural assumptions about the distribution of utility functions
encountered by the agent in her environment and derive the optimal bias that arises. We
relate these biases to stylized facts from psychology and behavioral economics. In the
illusion-of-control example, the agent overvalues her impact on her own well-being. In the
order-effect application, she exaggerates the quality difference among two available
objects observed in the first of the two periods. In the probability-weighting example we
revisit the model of Steiner and Stewart (2016), who derive the overweighting of small
probabilities as a second-best perception heuristic.

<hs>  Related literature</hs>
  ~~~~~~~~~~~~~~~~~~

Rate-distortion theory studies optimal communication via a noisy channel (Shannon, 1948,
1959). One of the primitives of this theory is an exogenous map that specifies a loss to
each input and output of the communication. A popular loss function is the square error.
In our paper, the loss function is derived from the agent's environment and is equal to
the average welfare loss caused by the distortion.2 Once we establish the relevant loss
function, we let the agent engage in optimal error management: she avoids the costlier
types of the errors. Beyond information theory, error management has been studied in
several scientific disciplines such as biology and psychology. See Johnson et al. (2013)
for an interdisciplinary literature review and Alaoui and Penta (2016) for a recent
axiomatization of the cost-benefit approach to error management within economics. We
contribute to this literature a formal characterization of loss from misperception based
on a statistical description of the agent's environment. Sims (1998, 2003) has introduced
an exogenous information-theoretic capacity constraint to economics. The subsequent
literature on rational inattention studies the information acquisition and processing of
an agent who, as in our model, is unsure about a payoff-relevant parameter but who, unlike
our agent, knows her payoff function. In that setting (assuming signal cost is
nondecreasing in Blackwell informativeness), the agent acquires only an action
recommendation and no additional information beyond that needed for choice. In our model,
the agent does not know her payoff function when she processes information and thus forms
beliefs beyond those needed for the mere action choice in any given problem. The resulting
optimal information structure can then be naturally interpreted as a perception of the
payoff parameter.3 Our assumption that the perception strategy is optimized across many
decision problems has appeared in the literature on the evolution of the utility
functions. This literature studies the performance of decision processes across a
distribution of the fitness rewards to the available actions. Depending on the constraints
assumed, the optimal decision criterion is either the expected utility maximization, as in
Robson (2001), or its behavioral variants, as in Rayo and Becker (2007) and Netzer (2009).
(See Robson and Samuelson, 2010 for a literature review.) Most of this literature focuses
on choice under certainty. Two exceptions who, like us, focus on the probability
perception are Herold and Netzer (2010), who propose that biases in probability perception
serve as a correction of another behavioral distortion; and Compte and Postlewaite (2012),
who conclude that an agent with limited memory benefits from ignoring weakly informative
signals. We contribute to the branch of the bounded rationality literature that emphasizes
limited memory. Mullainathan (2002) studies the behavioral implications of exogenous
imperfect memory usage. Like us, Dow (1991), Hirshleifer and Welch (2002) and Wilson
(2014) study the behavioral implications of an agent who optimizes her usage of limited
memory, but they examine effects that are different from ours. In his survey, Lipman
(1995) focuses on memory-related frictions. This paper generalizes the model of Steiner
and Stewart (2016), who study optimal probability perception in a choice between a binary
lottery with random rewards and a fixed outside option. The contribution of this paper
beyond Steiner and Stewart is threefold: (1) We significantly enlarge the class of
settings by allowing arbitrary payoff distributions and arbitrary action sets; (2) we
characterize the perception loss function from the more fundamental value of information
function, and (3) we deliver new behavioral insights. Two of our derived biases, the
illusion of control and overprecision, are classified among so-called positive illusions
(Taylor and Brown, 1988). Such positive belief biases are often rationalized by assuming
that the agent derives felicity from holding favorable beliefs about herself; see for
example Brunnermeier and Parker (2005), Caplin and Leahy (2001), and Köszegi (2006). In
contrast, belief distortions in our model are purely instrumental—they guide choice—and
arise in the absence of any felicity benefits. The paper is organized as follows. Section
2 introduces the model, and our loss characterization is presented in section 3. We
develop general results on the direction of biases in section 4, and applications in
section 5. We show an example of a sophisticated Bayesian agent in section 6. Section 7
concludes.

<h>A MODEL OF MISPERCEPTIONS</h>
-------------------------

Our aim is to characterize how the distribution of payoff functions u translates into the
loss function L.

<hs>  The role of v″</hs>
  ~~~~~~~~~~~~~~

The second derivative of the value function plays a central role in our analysis. Here, we
offer intuitive explanations of its role in our results.

<hs>  Illusion of control</hs>
  ~~~~~~~~~~~~~~~~~~~

The term Illusion of control, introduced by the psychologist Langer (1975), refers to the
overestimation of one's ability to impact one's own well-being. As an extreme example,
casino visitors may overestimate the relevance of their choices over payoff-equivalent
lotteries.

<hs>  Order effects</hs>
  ~~~~~~~~~~~~~

Psychologist Baron (2000) defines an order effect as order-dependent weighting of the
observed pieces of evidence when the order of the evidence presentation is normatively
uninformative. Primacy effect arises when the agent overweights her first impression and
the recency effect refers to overweighting the last impression. Page and Page (2010)
document the order effect in a field study of talent judgment and they argue for the
relevance of the effect in hiring practices. Here we offer a stylized model in which the
order effect arises as a second-best perception strategy for an agent with imperfect
memory. Our next result shows that the second-best perception avoids the relatively costly
types of error by a systematic exaggeration of the first impression.

<hs>  Overprecision</hs>
  ~~~~~~~~~~~~~

Proposition 3 together with Lemma 4 imply the direction of the bias.

<hs>  Overweighting of small probabilities</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We revisit here Steiner and Stewart (2016), who provide a microfoundation for
overweighting of small probabilities akin to the one in prospect theory (Kahneman and
Tversky, 1979). The purpose of the revisit is twofold. First, we show how the problem from
Steiner and Stewart can be solved by the general method from this paper. Second, we
contrast their model with the setting from the previous subsection in which
underestimation of small probabilities arises, and clarify the forces driving the opposite
biases in these two frameworks. Proposition 3 implies that overvaluation of small
probabilities arises in this setting.

<h>A SOPHISTICATED AGENT—AN EXAMPLE</h>
--------------------------------

The agent from section 4 is naive in that she does not fully utilize the information
available to her at the choice stage. This section studies the sophisticated perception
strategies of an agent who loses some information during the decision process, but who is
then fully capable of utilizing the information retained until the choice. Sophisticated
perception

<h>DISCUSSION</h>
----------

We have studied the cost of misperception in a model of decision making under uncertainty.
Our main technical result, Lemma 1, shows that the loss function can be entirely
characterized from the value function of the underlying decision problem. In our
applications, the decision problem is specified by a random payoff function, which makes
our environment rich enough. Note however that our loss formula applies to all settings,
whether or not the payoff function is random, as long as the value function admits a
second derivative. We presented a series of applications of this loss formula to settings
in which the agent has imperfect memory, and hence faces an error-management problem;
these examples allowed us to microfound several well-known behavioral biases.
Microfoundations for behavioral biases can contribute to normative discussions of
debiasing. Our model suggests that a bias relative to the precision-maximizing perception
may be second-best optimal and thus presence of a bias is not enough to justify an
intervention without further arguments. As the standard maladaptation argument goes, an
intervention into the decision process may be beneficial if the agent's environment has
changed since the biases have evolved. Interestingly, the model suggests that an
intervention may be justified even if the agent's environment has not changed since
adaptation took place. This is the case if an intervening outsider knows more about the
agent's decision problem than the perception designer—evolution—has known.


<h>REFERENCES</h>
----------

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  [25] C. E. Shannon. A Mathematical Theory of Communication. doi:10.1002/j.1538-7305.1948.tb01338.x
  [26] Herbert A. Simon. A behavioral model of rational choice. doi:10.2307/1884852
  [28] Christopher A. Sims. Implications of rational inattention. doi:10.1016/S0304-3932(03)00029-1
  [29] Jakub Steiner, Colin Stewart. Perceiving prospects properly. doi:10.1257/aer.20141141
  [30] Shelley E. Taylor, Jonathon D. Brown. Illusion and Well-Being: A Social Psychological Perspective on Mental Health. doi:10.1037/0033-2909.103.2.193
  [31] Andrea Wilson. Bounded Memory and Biases in Information Processing. doi:10.3982/ECTA12188
<ART>R&D networks and absorptive capacity in a Salop model
=====================================================

Authors: Luca Correani, Fabio Di Dio
DOI: 10.1016/j.rie.2019.03.001
Year: 2019  |  Pages: 123-128
ASJC codes: 2002
Keywords: Cooperation, R&D networks, Salop

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

The paper investigates the incentives of Salop-type oligopolistic firms to cooperate and the architecture of the resulting collaboration networks. We find that when spillovers are exogenous, firm profits are not affected by the network structure. On the contrary, with endogenous spillovers (absorptive capacity) firms tend to form less dense networks. We also seek out the architecture of socially efficient networks, showing that social welfare is maximised in the complete network. Also, given the network structure we conclude that a Salop industry could be characterized by a general tendency to under-connection.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Our key findings are as follows. First, in presence of exogenous spillovers, firm profits
are not affected by the network structure. Thus, empty or partially connected networks are
desirable as much as a complete network. Second, with endogenous spillovers (absorptive
capacity), firm profits decrease with the number of cooperation links. Therefore, there is
no private incentive to form dense networks (empty network). Third, independently of
whether spillovers are exogenous or endogenous, social welfare is maximised in the
complete network. The structure of the paper is as follows. Section 2 describes the model
and its properties. Section 3 presents the main results. Section 4 concludes.

<h>THE MODEL</h>
---------

In this section we present the main blocks of the model. We first introduce the
preferences (demand and supply side) then we account for the timing of the moves.

<hs>  Endogenous spillovers: absorptive capacity</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In a Salop oligopoly with imperfect information and endogenous spillovers (absorptive
capacity), firms’ profits decrease with the number of cooperation links.

<h>WELFARE ANALYSIS</h>
----------------

Proposition 3 states that link formation is always welfare improving. Specifically, in the
case of endogenous spillovers, there is a general tendency to under-connection with
respect to social welfare. This result may be explained as follows. In the case of
exogenous spillovers, forming pair-wise collaboration links keeps unchanged firm profits
(Proposition 1) but both reduces market price and increases consumer surplus. As a result,
social welfare increases. On the contrary, with endogenous spillovers firm profits
decrease as m increases (see Proposition 2). Nonetheless, this change is more than
compensated by consumer surplus increase, thus entailing a greater level of social
welfare.


<h>REFERENCES</h>
----------

  [1] Luca Correani, Fabio Di Dio. A note on link formation and network stability in a Hotelling game. doi:10.1016/j.orl.2017.04.008
  [2] Luca Correani, Giuseppe Garofalo, Silvia Pugliesi. R&D cooperation in regular networks with endogenous absorptive capacity. doi:10.1515/rne-2014-0007
  [3] F. Deroian. Dissemination of spillovers in cost-reducing alliances. doi:10.1016/j.rie.2007.12.004
  [4] Frédéric Deroian, Frédéric Gannon. Quality-improving alliances in differentiated oligopoly. doi:10.1016/j.ijindorg.2005.09.006
  [5] Sanjeev Goyal, Sumit Joshi. Networks of collaboration in oligopoly. doi:10.1016/S0899-8256(02)00562-6
  [6] Sanjeev Goyal, José Luis Moraga-González. R&D networks. doi:10.2307/2696388
  [7] Leo A. Grünfeld. Meet me halfway but don't rush: Absorptive capacity and strategic R&D investment revisited. doi:10.1016/S0167-7187(03)00076-6
  [8] Morton I. Kamien, Israel Zang. Meet me halfway: Research joint ventures and absorptive capacity
  [9] Dermot Leahy, J. Peter Neary. Absorptive capacity, R&D spillovers, and public policy. doi:10.1016/j.ijindorg.2007.04.002
  [10] Yasunori Okumura. Spatial competition and collaboration networks. doi:10.1007/s00182-011-0297-3
<ART>Redistribution by means of lotteries
====================================

Authors: Stéphane Gauthier, Guy Laroque
DOI: 10.1016/j.jet.2017.04.002
Year: 2017  |  Pages: 707-716
ASJC codes: 2002
Keywords: Incentives, Lerner egalitarianism, Random redistribution

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

A government designs anonymous income transfers between a continuum of citizens whose income valuation is privately known. When transfers are deterministic, the incentive constraints imply equal treatment independently of the government's taste for redistribution. We study whether random transfers may locally improve upon the egalitarian outcome. A suitable Taylor expansion offers an approximation of the utility function by a quasilinear function. The methodology developed by Myerson to deal with incentive constraints then yields a necessary and sufficient condition for the existence of a socially useful randomization. When this condition is met a large set of lotteries are locally improving. A special menu made of two lotteries only is of interest: all the agents with low risk aversion receive the same random transfer, financed by a deterministic tax paid by the high risk aversion agents.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

It is known that in a second-best world a principal may find it valuable to propose random
contracts to the agents. For instance, in the presence of asymmetric information, risk can
be used to relax the incentive constraints (Laffont and Martimort, 2002). In Gauthier and
Laroque (2014) we give a necessary and sufficient condition for useful/useless
randomization near a deterministic optimum, but our previous analysis only applies to
well-behaved problems where the constraints are qualified, i.e., the gradients of the
binding constraints at the optimum are linearly independent. In this note we deal with a
case where the constraints are not qualified. We consider a government that allocates a
given sum of money deterministically between potential recipients with different income
valuations. As observed by Lerner (1944) only equal sharing can be implemented if
valuations are not observed by the government and recipients always prefer more income to
less. The constraint set reduces to a single point and qualification is not met. In this
setup a random allocation may allow the government to screen individuals according to
their attitudes toward risk. Pestieau et al. (2002) provide a necessary condition for
local randomized redistribution to improve upon the equal sharing outcome. However their
proof uses a Taylor expansion where the variance of the lotteries is negligible and so it
does not give tools to design the optimal differential risk exposure. One contribution of
our note is to provide a class of expansions where the noise component is first-order non-
negligible. An appealing feature of this approach is that it enables us to apply the
standard quasilinear toolkit of contract theory developed by Myerson (1982). This yields a
necessary and sufficient condition for the existence of locally improving stochastic
allocations. The social weights put on the agents with the smallest risk aversions must be
large enough that a transfer in their favour more than compensates for the extra
randomness required to meet the incentive constraints. There are many ways to design the
locally improving randomizations. Still it turns out that there is no loss in generality
in limiting the attention to simple schemes that work as follows. The agents have to
choose between two (small) deviations from the status quo. One is a certain tax, the other
is a random transfer with positive expectation and variance. The deviations are built so
that all the agents with a risk aversion larger than a threshold choose to pay the certain
tax, while the agents with a smaller risk aversion take the other (risky) option. The
paper is organized as follows. Section 2 lays down the deterministic framework, which is
extended to a random environment in Section 3. Section 4 presents an example. Finally
Section 5 states and proves the main propositions.

<h>RANDOM REDISTRIBUTION</h>
---------------------

We extend the power of the government and allow for randomized redistribution. The
government can now design a menu of lotteries, such that every individual must choose some
lottery in this menu. Given the random draw from the lottery, there is commitment from
both the government and the players to conform to the outcome. Suppose also that a law of
large number holds, so that with independent draws the cost of the lottery is equal to its
mathematical expectation. With this class of small randomizations the variances of income
transfers explicitly enter the incentive constraints (7). In the absence of noise these
constraints reduce to (4) and prevent any income redistribution. Randomized income
transfers expand the set of possible redistribution schemes consistent with incentive
compatibility. Although the set of allocations consistent with incentive compatibility is
larger than what is seen in the deterministic Lerner world, incentive constraints restrict
possible redistribution. These restrictions, which follow from standard arguments, are
given in Lemma 1.


<h>REFERENCES</h>
----------

  [1] Stéphane Gauthier, Guy Laroque. On the value of randomization. doi:10.1016/j.jet.2014.02.006
  [2] Frøystein Gjesdal. Information and Incentives: The Agency Information Problem. doi:10.2307/2297362
  [3] Roger Guesnerie, Jean Jacques Laffont. A complete solution to a class of principal-agent problems with an application to the control of a self-managed firm. doi:10.1016/0047-2727(84)90060-4
  [4] Jean Jacques Laffont, David Martimort. The theory of incentives: The principal-agent model
  [7] Roger B. Myerson. Optimal coordination mechanisms in generalized principal-agent problems. doi:10.1016/0304-4068(82)90006-4
  [8] Pierre Pestieau, Uri Possen, Steven Slutsky. Randomization, revelation, and redistribution in a Lerner world. doi:10.1007/s001990100224
<ART>Regulations and location choices of top R&D investors worldwide
===============================================================

Authors: Antonio Vezzani
DOI: 10.1016/j.strueco.2019.04.005
Year: 2019  |  Pages: 29-42
ASJC codes: 2002
Keywords: Employment protection, Internationalisation, Multinational corporations, Product market regulation, Top R&D investors

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper explores how the interaction of different framework conditions affect the way in which top corporate R&D investors organise their cross-border operations worldwide. The analysis uses location-specific aspects, socio-economic factors and other controls common in the economic geography literature to investigate the distribution of a company's international subsidiaries. The location drivers are estimated using a multilevel mixed-effects logistic regression, controlling for both country characteristics and company specific random effects. Our results confirm that framework conditions, as product market regulation (PMR) and labour market legislation (EPL), affect the location strategies of top R&D investors. Adding to the literature we also found that: (i) PMR and EPL exert a mutually reinforcing negative effect on the location of subsidiaries, (ii) the effect of EPL is not significant for low levels of PMR, and (iii) barriers to trade and investment is the PMR component with the largest negative effect. Policy implications are drawn accordingly.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The policy debate on the European economic recovery is currently focusing on one key
question: will the European economy be able to generate a self-sustained and balanced
expansion once the three temporary tailwinds that have sustained its recent performance —
the sharp fall in oil prices, a supportive macro-economic policy and the depreciation of
the euro's exchange rate — have died down? To answer this question, both the shortfall of
investment over the past few years, which has reduced the EU economic growth potential,
and the declining trend in EU productivity growth, which has not yet been reversed, must
be carefully considered. This calls for a reboot of growth drivers — such as productivity
and innovation — to ensure a sustainable recovery and to prevent reverting to a situation
of consistent weak growth. The Investment Plan for Europe1 launched at the end of 2014 by
the European Commission represents a first step in this direction. In addition to
providing a financial commitment, the plan has a long-term relevance for innovation and
productivity growth because of its ‘third pillar’, which aims to create an investment-
friendly environment. The underlying rationale of this pillar is that providing greater
regulatory predictability, removing barriers to investment across Europe and further
reinforcing the Single Market (i.e. creating optimal framework conditions) will unlock the
full potential of investment in Europe, including investment in research and development
(R&D). Accordingly, ‘more efficient labour and product markets’ are recognised as key
policy priorities in the Five Presidents’ Report (European Commission, 2015a; p.7).
Finally, the European Commission communication “A renewed European Agenda for Research and
Innovation — Europe’s chance to shape its future” stress the importance of stimulating
private investment in R&D and of regulation that provides the right environment to promote
innovation (European Commission, 2018). Against this background, and being aware that
fostering private R&D investment in Europe is essential to revitalise EU innovation
performance, this paper analyses the impact that third-pillar-relevant variables have in
shaping the organisation of top R&D investors cross-border activities worldwide. Namely,
we test whether changes in the level of regulation in product and labour markets — and
their possible interplay — have an impact in attracting foreign long-term investments. In
doing so, we investigate the role that structural policies play in shaping firms’ location
decision, as Aghion et al. (2005, 2009) did for their effects on innovation and
productivity. To this end, we use the 2014 EU Industrial and R&D Investment Scoreboard
(Hernández et al., 2014) dataset, collecting information on the top 2500 R&D investors
worldwide and their ownership structure. In the empirical application, we model the
probability of a company international subsidiary to be located in a particular country
upon location-specific regulatory framework conditions, socio-economic factors, and other
controls commonly used in the economic geography literature. The location decision drivers
are estimated using a multilevel mixed-effects logistic regression, controlling for both
country characteristics and company specific random effects. Following previous empirical
literature in the field (e.g. Aghion et al., 2005), the synthetic indicators EPL
(employment protection legislation) and PMR (product market regulation), provided by the
Organisation for Economic Co-operation and Development (OECD), are used to characterise
rigidities in the labour and product markets, respectively. From an economic point of
view, well-functioning labour and product markets (able to absorb shocks and allocate
resources in favour of the most productive and innovative firms) and lower administrative
costs should help foster innovation and attract (and/or increase) investment in knowledge-
based capital (OECD, 2013a) through the creation of a friendlier business environment. In
fact, the effectiveness of the wider innovation system often hinges on the quality of
framework conditions and the capacity to ensure an innovation-friendly climate in both
more and less R&D-intensive parts of the economy (European Commission, 2015b). The
remainder of this paper is organised as follows. Section 2 briefly reviews the literature
on the role of well-designed framework policies in promoting innovation through the
creation of a business-friendly and attractive environment and in influencing the location
decisions of R&D-intensive multinationals; this is done with a specific focus on the
empirical studies using PMR and EPL. Section 3 discusses the dataset and methodology
employed for the empirical analysis. Section 4 presents a short descriptive analysis of
the geographical location of the companies in the sample and comments on the results of
the econometric analysis. Section 5 summarises the main results and presents the major
policy implications. Section 6 briefly concludes.

<h>THEORETICAL FRAMEWORK</h>
---------------------

The capacity to attract high-value FDI from knowledge-intensive and innovative
multinationals is a key element for sustained growth as, especially in advanced knowledge-
based economies; frontier innovation has become the main source of growth (Aghion and
Griffith, 2005). In this context, multinational corporations (MNCs) have become central
economic actors because of their large international investments and numerous foreign
subsidiaries, which enable them to shift activities within their multinational network
according to changing conditions. The literature on countries’ attractiveness in terms of
international investment and location factors is broad and diverse and has not yet
resulted in many clear-cut policy implications. Stated simply, a single theory explaining
the location decisions of MNCs is still lacking, and a variety of models attempting to
explain such decisions emphasise different drivers, getting also to different results.2
Among the drivers affecting the location decisions of MNCs, we pay special attention to
the role of competitive product and labour markets. These have emerged as particularly
relevant factors taken into account by technological leaders (Belderbos et al., 2008).
Accordingly, in what follows we briefly summarise the most relevant findings of the
empirical literature regarding the expected effects of product market and labour
regulations on firm strategic decisions and performance. In doing so, our theoretical
reference will be the Schumpeterian innovation paradigm. In a Schumpeterian framework,
growth is driven by innovative firms introducing quality-improving innovations within the
economy that tend to displace previous technologies. In this context, growth involves a
conflict between old and new technologies and old and new skills. Structural policies —
such as product market liberalisation and/or labour market flexibility — may have a role
in facilitating this process of creative destruction (Aghion et al., 2005, 2009) by
favouring a business-friendly environment. In other words, the Schumpeterian creative
destruction process seems to be favoured by a dynamic business environment.3 This can be
reached by setting framework conditions that, for instance, allow young innovative firms
to easily enter a market and grow — without facing impeding regulation barriers — and
allow inefficient firms to exit the market, freeing resources for those that stay in
business. Moreover, the typically long-term character and high volume of investment
involved in setting up a subsidiary abroad makes the stability of the regulatory framework
a crucial factor. In the presence of high administrative entry costs, stringent PMR and
EPL, this reallocation of resources may be less efficient, damaging the most innovative
and productive firms and sectors (European Commission, 2015b). Aghion et al. (2005)
empirically tested the Schumpeterian theory on the relationship between product market
competition and innovation rate. They showed the existence of an inverted U-shaped
relationship between product market competition and innovation. This implies the presence
of an ‘escape competition effect’ at lower levels of product market competition, while the
aforementioned ‘Schumpeterian effect’ — pointed out in earlier endogenous growth models
and in the industrial organisation literature4 — dominates at high (but not too high)
initial levels of product market competition.5 Therefore, although competition may
increase the incremental profit from innovating, it could also reduce innovation
incentives for laggards.6 The increasing body of literature and empirical research
analysing the effect that changes in the level of PMR have on economic performance through
the process of entry and exit also focuses on the final effect that this has on
productivity (Conway et al., 2006). Scarpetta et al. (2002) found that the overall PMR
level (and, in particular, administrative barriers to start-ups) has a significant
negative impact on firm entry (see also Brandt, 2004). Blind (2012) studied the impacts of
six different regulatory framework conditions on the innovation performance of a set of
OECD countries, finding mixed results. Using OECD data, Bourlès et al. (2013) showed that
stringent PMR has a negative indirect effect on total factor productivity, especially for
countries close to the productivity frontier. This negative effect is mainly transmitted
through investments in R&D and ICT (Cette et al., 2017), and operate along with a negative
direct effect on production prices and wages Cette et al. (2014). Accordingly, Franco et
al. (2016) found that PMR has a negative impact on R&D efficiency and the magnitude of
this impact changes along the distribution of PMR. Amable et al. (2009) study the effect
of market liberalisation (proxied with PMR) on innovation and productivity, finding that
this is positively related to productivity the closer we get to the technological
frontier. Barbosa and Faria (2011) study the impact of PMR, EPL, intellectual property
rights and credit access on innovation intensity at industry level using CIS data. They
find a negative effect of PMR and EPL on sector innovativeness. Andrews and Criscuolo
(2013) relate allocative efficiency to framework policies, such as the level of
administrative burdens on start-ups and the cost of closing a business, and to the level
of EMP. Looking at OECD countries, Barone and Cingano (2011) study the effect of high
levels of PMR the service sector on the performance of manufacturing industries heavily
relying on them finding a negative relation. Along this line, Canton et al. (2014) found
that a less strict PMR that applies to professional services, which are increasingly and
intensively used by knowledge-intensive manufacturing firms (Ciriaci and Palma, 2016),
improves business dynamics and, as a result, firms’ ability to allocate resources
efficiently. For economies to thrive on innovation, labour also needs to be reallocated
within and across firms and sectors. In a constantly changing economic context and/or with
the introduction of labour-saving technologies, labour market frictions may generate
inefficient labour allocation and unemployment for specific skills. In these cases, a
stringent EPL may hinder the redirection of resources towards the most productive uses and
delay the match of labour supply and demand. In line with this expectation, high EPL may
reduce R&D investment, hampering the growth of innovative firms that are in need of
skilled personnel and complementary resources to implement and commercialise their
innovations (Andrews and Criscuolo, 2013; Amoroso et al., 2015). Similarly, Bassanini et
al. (2009) find a negative impact of layoff restriction on aggregate labour productivity
growth in OECD countries. Cingano et al. (2010) analyse the impact of EPL and financial
market imperfections on investment, capital-labour substitution, labour productivity and
job reallocation at firm level, finding a negative relationship with differences depending
on the sector considered. Calcagnini et al. (2014) use EU firm level data for the period
1994–2000 (from Amadeus) to study the impact of labour regulation on firm investment
decisions, finding a negative relationship. Similarly, Griffith and Macartney (2014) study
the impact of EPL on innovation activity, finding that MNCs locate innovation activity
mainly in countries with low EPL. Some studies go beyond the usual approach of considering
the different types of regulations and barriers as independent factors by introducing an
interaction term in their empirical setting. The interaction term allows considering
possible mutually reinforcing effects among the different types of regulations. Égert
(2016) uses OECD country level data to study the drivers of multifactor productivity,
looking in particular to market and employment regulations. He finds an inverse
relationship between high regulations (both market and employment) and multifactor
productivity. By interacting the market and labour regulation proxies he uncovers a
differential impact of market regulation depending on the level of labour regulation.
Amable et al. (2011, 2016) perform a country level analysis on the relationship between
product market and labour regulations and unemployment, also using an interaction term
between the two regulation proxies. They found EPL and PMR are substitute rather than
complementary policies.7 Our paper aims to contribute to this literature by verifying the
extent to which differences in the strictness of regulation (in both product and labour
markets) affect the location strategy of R&D-intensive multinationals. In particular, we
test whether environments characterised by lower levels of product and labour market
regulation are indeed more attractive to R&D-intensive multinationals looking for dynamic
innovation ecosystems and market conditions that favour returns to their innovative
investments. Moreover, we explore possible joint effects of employment and PMR on firms’
location decision. Despite the scant literature on this mechanism, we may presume that
high PMR and EPL have a mutual reinforcing effect in reducing country attractiveness for
R&D intensive MNCs. However, we do not have sufficient elements to determine ex-ante
whether this effect would be relevant; we let the empirical analysis disentangling the
significance and strength of this mechanism. Apart from PMR and labour market regulation,
many other socio-economic factors may influence the strategic location decision of MNCs.
Besides firm-specific characteristics, such as firm size and corporate performance, sector
and technological intensity, other important drivers in the host country have been
identified as particularly relevant. These include: (i) administrative burden (i.e. red
tape), (ii) market features, such as size, growth potential and purchasing power; (iii)
the presence of high-quality scientific infrastructure and human resources; (iv) the
presence of tax breaks and government support, and the strength of intellectual property
protection; and (v) geographical, technological and cultural distance between the source
and the destination country.8 When looking at the relationship between PMR, EPL and firms’
location decisions, we will also considering these factors.

<hs>  The database</hs>
  ~~~~~~~~~~~~

The empirical application is based on the EU Industrial R&D Investment Scoreboard 2014
data (Hernández et al., 2014, http://iri.jrc.ec.europa.eu/scoreboard.html), which contains
economic and financial information for the world's top 2500 corporate R&D investors. It is
based on company data taken directly from companies’ annual reports.9 Each of these top
2500 R&D companies invested at least €15.5 million in R&D in 2013. Information on the
subsidiaries of these top R&D investors was obtained by matching the Scoreboard dataset
with the ORBIS databank of Bureau van Dijk, and reconstructing the corporate structure of
the Scoreboard companies in place at the end of 2014. We were able to identify 218,343
industrial subsidiaries10 belonging to 2,338 of the top corporate R&D investors worldwide.
Unfortunately, ORBIS does not report location or main sector of activity for all these
subsidiaries. Only those for which both location and main sector of activity were known
were included in the analysis. The final number of subsidiary companies included in the
analysis is 140,382, belonging to 2,288 out of the top 2,500 corporate R&D investors
worldwide.11 The Scoreboard dataset has been merged with data on PMR and EPL from the
OECD. PMR is constructed with a bottom-up approach, through rounds of aggregation of
different indicators, in which each component of the regulatory framework is equally
weighted. The components of the PMR summary index are three composite indicators: (1)
state control; (2) barriers to trade and investment; and (3) barriers to entrepreneurship.
‘State control’ measures the extent of public ownership in the economy and the involvement
of the state in business operations (e.g. via controlling prices). ‘Barriers to trade and
investment’ is the intensity of explicit (like barriers to FDI) as well as other barriers
to trade and investment (e.g. the existence of a differential treatment for foreign
suppliers). Finally, the indicator ‘barriers to entrepreneurship’ captures the complexity
of the regulatory procedures, the administrative burdens on start-ups and the regulatory
protection of incumbents. Data used to calculate PMR come from a questionnaire sent to
governments in OECD and non-OECD countries (see Koske et al., 2015, for a full description
of the methodology used to construct the PMR). It should be noted that, although being the
only comprehensive, rich and comparable across countries available indicator on product
market regulation the PMR does not capture all regulatory barriers, but only a selection
of them. Therefore, it provides a partial approximation of the regulatory framework in
each country. The EPL indicator measures the procedures and costs involved in dismissing
individuals or groups of workers and the procedures needed to hire workers on fixed-term
or temporary work agency contracts. The EPL is constructed as a weighted average of 21
items covering different aspects of employment protection regulations (as they were in
force on 1st January of each year), which can be classified in three main areas: (i)
protection of regular workers against individual dismissal; (ii) regulation of temporary
forms of employment; and (iii) additional, specific requirements for collective dismissals
(see OECD, 2013c for details and the specific weights applied to each item). PMR and EPL
indicators measure product and market regulation on a 0–6 scale respectively; higher
values represent a stricter regulation. We retrieved data on the administrative cost of
starting a business and on the level of taxation on profits from the World Bank's Doing
Business dataset, which allows cross-country comparison in a field where available (and
comparable across time and countries) data are very limited. The cost of starting a
business records the procedures officially required, or commonly carried out in practice,
for an entrepreneur to start up and formally operate an industrial or commercial business,
as well as the time and cost to complete them and the paid-in minimum capital
requirements.12 Differently from ‘barriers to entrepreneurship’, which measure the
complexity of the regulatory framework, the cost of starting a business tries to quantify
the associated costs to a new venture, providing a slightly different information. We also
include the Park–Ginarte index to control for the strength of intellectual property rights
protection, which in turn is related to the R&D and innovation activities of a country
(Ginarte and Park, 1997) and to the possibility for innovative MNCs to protect from
imitation. From the World Development Indicators we extract data on gross domestic product
(GDP), trade and unemployment to control for the macro-economic condition of a country.
Finally, as is common in the relevant empirical literature, we also used a series of
geographical and cultural distance measures provided by the GeoDist database, which was
developed and described by Mayer and Zignago (2005, 2011).13

<hs>  The econometric strategy</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~

This setting allows a more appropriate modelling of a firm decision to locate in a given
country by directly dealing with the clustered structure of the data, where each cluster
has its own choice behaviour. Indeed, in the present setting, instead of considering all
observations at once, these are organised as a series of N independent clusters
(companies) nested into I different clusters (industries). A similar setting has been used
by Basile et al. (2008) to analyse the subsidiary location of multinational firms in 50
European regions, and by Griffith et al. (2014) to ascertain the importance of corporate
income taxes in determining where firms choose to legally own their intellectual property
rights. Among the drivers of a company location decision, xci, we included (i) the third-
pillar relevant variables discussed above, PMR and EPL; (ii) country controls: cost of
starting a business, tax rate on profits GDP level, differences in per capita GDP between
source (headquarter location) and destination country, trade as a share of GDP,
unemployment rate; and (iii) geographical controls: distance in kilometres between the
capital of the hosting country and original country location of the Scoreboard company,
and sharing a common language (binary 1/0). It is worth noting that, as PMR emerged as the
main determinant of such a probability, we decided to analyse also the impact of its three
components, i.e. state control, barriers to trade and investment, and barriers to
entrepreneurship. Among the country controls, we had initially also included the share of
people with a tertiary education, but, as results were confirmed and its insertion caused
a large drop in the number of observations (especially because of missing data for China),
we excluded it from the final estimations (results are available upon request). PMR values
are available every 5 years (the last available year is 2013). In our analysis we used the
average value between 2008 and 2013. The same holds for the high-level indicators (state
control, barriers to entrepreneurship and barriers to trade and investment), whereby the
simple average constitutes the value of PMR. However, EPL values are available yearly, and
we used the average for the period 2008–2012. For the cost of starting a business
(expressed as share of income per capita) we used the average from 2008 to 2012.14 Apart
from EPL, PMR (and its three components) and common language, all the variables are
expressed in logarithms. Table A1 (in the Appendix) shows the descriptive statistics for
the explanatory variables.

<hs>  The identification strategy</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~

Before discussing the estimation results, we deem important discussing the limitation of
our approach and the mitigation strategy we take to try identifying the correct parameters
of the model. Indeed, the identification of the parameters associated to PMR and EPL
requires that governments’ decisions with respect to employment and market regulation are
independent from firms’ location choices. In part, we rely to the fact that the decision
of locating in a new country may take years (from the conception to its
operationalisation) and that therefore the linkage from environment to location is the one
more likely to have the higher signal to noise ratio. However, we also try to control for
the possible influence a multinational may have on governments’ decisions. Industry level
studies using PMR or EPL (e.g. Bassanini et al., 2009; Barone and Cingano, 2011) address
the possible reverse causality issue using a ‘double difference’ approach mutated from the
financial literature (Rajan and Zingales, 1998). This approach relies on the assumption
that industrial sectors in different countries have similar characteristics. This
homogeneity allows taking the differences of some characteristic of interest (e.g. how
much each sector relies on external financing) between sectors in a benchmark country
(typically the US) and use them as reference for the other countries. The exogenous
differences so observed in the benchmark country are used to characterised the industrial
sectors in the other countries (hence the ‘double difference’ approach), and then the
analysis on the variable of interest is run. For example, Bassanini et al. (2009) use the
different propensity to layoff among the US industries as reference for the other
economies when analysing sectoral productivity growth. Our focus on firm data (rather than
industry data) makes this approach not particularly suitable for the analysis. Indeed, the
assumption of an industrial homogeneity across countries is excessively restrictive in a
framework dealing with large multinationals presenting a persistent heterogeneity in their
investment strategies (Montresor and Vezzani, 2015b; Coad, 2019). We therefore try to
replicate the country/sector arguments in line with our theoretical framework. In
particular, we control for the number top R&D investors operating in a specific sector and
headquartered in a given country. Local companies — and in particular large multinationals
— might have stronger linkages (and influence) on government decisions than foreign
companies operating in the same sector and that may consider locating there. However, this
variable may also represent a measure of the innovative capabilities of the
industry/country. For this reason we also control for the GDP of the potential hosting
economy. Again, while this measure may capture market determinants — larger markets may be
considered more valuable by firms —, it also controls for the possible influence a foreign
company might have on government decisions: larger economies are less susceptible to
foreign influences. Furthermore, we run a series of robustness checks using specific
exclusion restrictions (results are reported in Table A3 of the appendix). In particular,
we first include the number of scoreboard companies headquartered in a given country and
operating in a different sector from the foreign company that might potentially locate
there (column 1). We then exclude from the estimations the 5% most internationalised
companies (in term of number of countries in which they operate): being particularly
globalised, these companies are more likely to move subsidiaries across countries and
therefore might have an actual leverage on countries’ regulation decisions (column 2). We
finally exclude countries not hosting a Scoreboard company headquarter (column 3). A part
from this last estimation, which is particularly restrictive because basically keeps only
the most advanced economies, the results with respect to EPL and PMR are not statistical
different across all the estimations. All-in-all, these results suggest that our
parameters are correctly identified.

<hs>  Where do top R&D intensive multinationals locate?</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Out of the 2,500 companies present in the R&D Scoreboard, we managed to find information
on subsidiaries for 2,288 of them. For these companies we considered only those
subsidiaries that are not branches (as Castellani et al., 2017) and for which we could
retrieve information on the sector of activity. Therefore, the final number of subsidiary
companies included in the econometric analysis is 140,382, of which 89,940 (64.1%) are
‘international’, that is subsidiaries located in a country different from the one where
the Scoreboard parent company headquarter is located (see Table 1). International
subsidiaries located in the EU represent 58.3% of all subsidiaries, 10.3% are in the US,
1.5% in Japan and 2.7% in China (the remaining 27.2% are located in the rest of the
world). Looking at the top countries where the Scoreboard companies locate their
international subsidiaries, 56.7% are found in only 10 countries (see Table 2), a level of
concentration that is lower than that for Scoreboard headquarters. Some interesting facts
emerge if we compare the number of Scoreboard headquarters in a country and the number of
international subsidiaries of other Scoreboard companies located in the same country. If
we take the first 10 countries by number of international subsidiaries, only seven of them
are also among the first 10 countries by number of Scoreboard headquarters. Spain, Canada
and Mexico account for very few headquarters but many subsidiaries. For Canada, and
especially for Mexico, this can depend on how close ties are to the US, as these three
countries are part of a free trade agreement. As regard Spain, this observation can be
explained by the general high level of attractiveness of this country for FDI during the
1990s and the 2000s — at least until the financial crisis (see, e.g., Barrios et al.,
2004; Rodriguez and Pallas, 2008; Guimón, 2009). In contrast to the above, Switzerland,
Sweden and Japan are in the top 10 for number of Scoreboard headquarters but are in a
lower position on the chart for Scoreboard subsidiaries. The position of Sweden does not
come as a surprise, given the size of its internal market. In the case of Switzerland —
host to many pharmaceutical and financial multinationals — the explanation may reside in
the way we count subsidiaries: considering only industrial ones and not branches, which is
the kind of subsidiary that is typical of financial MNCs. Finally, the reason why Japan is
at the bottom of the top 20 destination countries chart may be the historical closed
nature of the Japanese market and its onerous institutional rules (see Nakamura and Oyama,
1998). So it comes as no surprise that Japan is the country with by far the highest number
of national subsidiaries (11,525), accounting for 22.8% of all national subsidiaries of
the Scoreboard companies included in the analysis. This is in line with the so-called
‘home bias’ of major Japanese R&D intensive firms (Belderbos et al., 2013). A similar
picture emerges when the number of Scoreboard companies headquartered in a particular
country is compared with the number of Scoreboard companies present in the same country
through one or more of their subsidiaries. Some countries, such as Spain and Canada,
register a much higher presence of Scoreboard companies than might be expected if only the
number of headquarters is considered. Before moving to the empirical application, we look
for descriptive evidence supporting our hypothesis of the role played by regulatory
framework in the location decision of companies. In Table 3, we report the pairwise
correlation coefficients between the number of international subsidiaries located in
country i, and our main variables of interest, PMR and EPL and the other framework
conditions considered in this study. Table 3 shows a statistically significant negative
correlation between the level PMR and the presence of international subsidiaries of
R&D-intensive Scoreboard companies. Also, the level of labour market regulation is
negatively correlated with the presence of international subsidiaries and positively with
PMR, but in both cases the coefficients do not appear to be significant at the standard
statistical level. The patent protection index is instead positively correlated with the
presence of international subsidiaries and negatively with PMR.

<hs>  Econometric analysis</hs>
  ~~~~~~~~~~~~~~~~~~~~

The estimation results for the different specifications used are reported in Table 4
(columns 1–4). First we include PMR and EPL, the variables discussed in the identification
strategy and geographical controls (column 1). Then we introduce the interaction between
EPL and PMR (column 2) and later all the other control variables, including cost of
starting a business, corporate income tax and patent protection index (column 3). Finally,
we report the results on an estimation excluding unemployment and trade (column 4). This
accounts for the possible impact of PMR and EPL on unemployment and trade; given their
effect on the probability of location may be underestimated if part of it goes through
these variables.15 The specification reported in column 4 is our reference model and we
use it also to identify which component of the PMR indicator — which emerged as much more
relevant than EPL — is the most influential (Table 6). From a policy point of view, this
analysis would help not only to detect which of the two aforementioned third pillar
relevant variables affects the most the kind of investment considered here (the presence
of a subsidiary in the country), but also to rank the different possible reforms in terms
of their potential impact. Before discussing the general estimation results, a caveat
should be pointed out. As no information was available on the year when the subsidiary was
opened, a lack of data common to many studies in the field, identifying causal relations
is not straightforward. However, our econometric analysis aims not to explain the decision
to open a subsidiary in a particular year, but to analyse the correlation between a
multinational's decision on how to organise its worldwide activities and a series of
country characteristics and geographical variables. These variables are those likely to be
considered when such a decision is taken and/or when the mother company decides whether or
not to stay in a particular host country. The majority of these characteristics are
structural and display a low degree of variation over time. Nonetheless, we use average
values over a 5- or 6-year period for our main variables of interest, and a 1-year lag for
the controls. Finally, it should be recalled that, as we use a particular class of
logistic estimator, the coefficients attached to our regressors could not be interpreted
as elasticities. In order to quantify the effects of our main variable of interest (PMR
and EPL) on the location conditional probabilities we will compute and comment their
marginal effects.

        The effects on location probability of top R&D multinational for third-pillar relevant variables

        Our results confirm that product and labour market regulations significantly
        affect the location probability of top R&D multinationals (Table 4). However, the
        coefficient attached to EPL is not statistical significant when its interaction
        with PMR is not taken into account. This is an interesting result pointing to the
        importance of considering the joint effect of the two framework conditions
        addressed in this paper. In the baseline specification (column 1 of Table 4), the
        PMR indicator is negative and significant, while the EPL is not. In the following
        specifications (columns 2–4) we include the interaction term between PMR and EPL.
        This makes meaningless the simple reading of the individual coefficients of the
        two indexes. To ascertain their overall impact on location decision we will
        compute the marginal effects later on. What is important noticing here is the
        coefficient capturing the interaction effect between PMR and EPL, which is
        negative and significant also when additional controls are included. This means
        that PMR and EPL do not have independent effects on the location choices of our
        firms. This result is in line with Aghion et al. (2009) that, exploiting a macro-
        panel data for OECD countries, found that the interaction between PMR and labour
        market rigidity explained a major part of the total factor productivity growth of
        countries close to the technological frontier, the effect of EPL being
        significantly lower if considered on its own. Moreover, our results suggest that
        there can be a certain value of the PMR above which the EPL becomes a significant
        negative explanatory variable of the location probability, an aspect that will be
        dealt with in more detail later. All the country controls included are significant
        and enter the equation with the expected signs. In addition, in line with previous
        empirical evidence (e.g. Barrios et al., 2012), the cost of starting a business16
        and the tax rate on profits show a significant negative correlation with the
        probability of locating in a particular host country.17 As expected (Hall, 2011),
        the patent protection index enters with a positive and significant coefficient.
        Also the two variables discussed in the identification strategy, GDP and # of SB
        headquartered (in the same sector) enters with a positive sign: the market
        potential of a country as well as the presence of national top R&D investors may
        attract further knowledge investments. Our companies also tend to favour countries
        with levels of GDP per capita lower than the source country. As far as the
        included geographical controls are concerned, we found that distance from
        headquarters negatively affects the probability of locating subsidiary activities
        in a given foreign country. In fact, the relative estimated coefficients are
        negative and strongly significant for all the specifications. On the contrary,
        sharing a common spoken language affects it positively. In fact sharing a language
        increases the efficiency in transferring and aggregating knowledge (Grant, 1996).
        The importance of this factor makes particular sense in the case of knowledge-
        intensive companies, such those in this analysis. As we said, because of the
        interaction term between the PMR and EPL indicators, the signs of the individual
        coefficients reported in columns 2–4 cannot be directly interpreted. What counts
        are their overall marginal effects, which considers also the interaction term.
        Therefore, we have computed the overall marginal effects for EPL, PMR and the
        other variables proxying the framework conditions of a country. Results are
        reported in Table 5. The marginal effect of PMR is much larger than that of EPL,
        indicating that PMR have a higher influence on the location decisions of
        R&D-intensive multinationals than employment protection. More specifically, a
        1-point increase/decrease in the PMR indicator decreases/increases the probability
        of choosing a particular location by 16.4%. The same increase in the EPL indicator
        decreases said probability by 1.8%. This effect is similar in magnitude and sign
        to the one of corporate income tax, while the cost of starting a business plays a
        minor role. The marginal effect of the patent protection index is instead positive
        and particularly relevant (18.4%). The last two results are not surprising given
        that we are dealing with R&D intensive MNCs, which may be more concerned about the
        creation and exploitation of knowledge assets rather than the administrative cost
        related to starting a new business. Because of the non-linearity of the logit
        model, and to better exploit the interaction between EPL and PMR, we also computed
        the marginal effects of each of these two variables for different values of the
        other one (Fig. 1). As anticipated, the non-significance of EPL in the baseline
        specification (where EPL and of PMR are considered separately) allows the
        identification of a threshold value of PMR above which EPL becomes significant in
        determining the location probability. Fig. 1 reports the marginal effects of PMR
        and EPL (lines) alongside the distribution of EPL and PMR (bars), respectively.
        The negative impact of PMR on the location probability increases as the level of
        EPL rises (left panel). This means that the higher the level of EMP in a given
        country, the greater the negative marginal effect of PMR on location probability.
        This reinforcing mechanism is similar to the one found by Fiori et al. (2012)
        studying the effect of PMR and employment protection on the employment rate of
        OECD countries. More interestingly, for low levels of PMR, the effect of EPL on
        the same probability is null and eventually positive (right panel). In sum, the
        higher the level of PMR, the higher the negative effect of employment protection,
        and vice versa. Fig. 1 also shows that some countries — USA and New Zealand — have
        levels of EPL notably lower than the rest of the sample, while others — China and
        India — have levels of PMR notably higher. As a further robustness check, we have
        run our main specification excluding these countries. Our main results are not
        influenced by the inclusion or exclusion of these countries (see Table A4).

     <hss>The effects of the different components of PMR</hss>

        Given the prominent role of the level of PMR emerged in the analysis, being the
        PMR index used a composite indicator (see Section 3.1), we also explore which one
        of its three main components — State Control, Barriers to trade and investment,
        and Barriers to Entrepreneurship — has the greater influence on the location
        probability. Table 6 reports the estimations using the full specification used in
        Table 4 (column 4), including separately the three components of PMR as
        explanatory variables and their interactions with the EPL composite indicator. The
        three columns of Table 6 report the coefficients of the independent variables,
        each including a different component of PMR in the set of explanatory variables.
        Since signs and significance of all the control variables do no change compared to
        the main estimation (Table 4), we will comment only the results for the components
        of PMR. As before, the presence of the interaction term between EPL and the PMR
        components (a different one for every specification) makes the simple reading of
        the individual coefficients’ signs and magnitude misleading. Therefore, Fig. 2
        reports the overall marginal effects at the mean values of the three PMR
        components. Barriers to trade and investment is the component with the greatest
        negative impact on location probability (−13.6%), followed by state control
        (−10.4%) and by barriers to entrepreneurship (−4.2%). Barriers to trade (such as
        differential treatment of foreign suppliers) and investments, and excessive state
        control (which may lead to unfair competition from state-owned enterprises) have a
        much greater effect on the probability of an MNC's subsidiary to be located in a
        particular country than barriers to entrepreneurship. This latter component may be
        more hampering for local entrepreneurship, eventually limiting competition and
        thus favouring local and foreign MNCs. However, the negative effect we found
        suggests that foreign MNCs still valuate negatively this type of obstacles.

<h>DISCUSSION AND POLICY IMPLICATIONS</h>
----------------------------------

Our results confirm previous empirical evidence showing that R&D-intensive MNCs tend to
locate their international activities in countries with greater market potential, head-
start opportunities and the right environment to create and exploit their knowledge
assets. Companies prefer to move into countries close rather than far away from their
headquarters. They also choose the location for their international activities on the
basis of cultural factors, such as a common language. This could make the task of sharing
and integrating technical knowledge (often tacit) easier, which would lead to lower costs.
The empirical evidence confirms that product and labour market regulations significantly
affect the location decision of top R&D investors’ subsidiaries. However, when taken
separately, EPL does not appear to play a significant role in such choices. When
considering instead the interaction between EPL and PMR, the former becomes significant,
while the latter has the greatest negative effect on companies’ location decisions. These
results show that these two regulations exert a mutually reinforcing negative effect on
the decision of top R&D investors about where to locate their subsidiaries. In other
words, the lower the level of PMR, the lower the negative effect of employment protection
and vice versa. Translated into policy terms, these results suggest the importance of
bearing in mind both markets when considering possible reforms of one of the two. The
interplay between PMR and EPL calls for integrated/coordinated policies in the two realms.
While the effect of PMR on location decisions is negative for each level of EPL, the
latter does not exert a significant effect for low levels of PMR. Our setting allows us to
identify the threshold level of the PMR index (1.5) below which EMP has no relevant effect
on the location decision of top R&D investing MNCs. In Fig. 3 we rank the EU-28 countries
according to their average PMR level in 2013, from the highest to the lowest, and report
the aforementioned threshold value. The sample of countries is divided into two groups,
above (left) and below (right) the threshold. A reduction of their PMR in countries above
the threshold (Lithuania, Sweden, Malta, Bulgaria, Latvia, Poland, Cyprus, Romania,
Slovenia, Greece, and Croatia) would mitigate and eventually neutralise the direct
negative effect of EPL on location decision. Clearly, this does not imply that those
countries below the threshold would not benefit from a reduction of PMR, as the
coefficient attached to the PMR indicator is always negative and significant. As already
said, our finding does not rule out the possible beneficial effect of reducing EPL. A
reduction of EPL would decrease the negative conditional effect of PMR on location
decisions (Fig. 1). Among the different components of the PMR index, barriers to trade and
investment have the greatest impact on location decisions, followed by state control and
barriers to entrepreneurship. By lowering barriers to trade and fostering investment, EU
policy-makers may facilitate the market uptake of new products and have the greatest
impact in attracting foreign investments. The cost of starting a business and the
corporate income tax rate also play a negative role on companies’ location decisions.
However, their effect is lower than that of the other two framework conditions discussed
above. The decisions of the companies considered in our study seem to be driven more by a
desire to improve efficiency than by cost reduction considerations. This seems supported
also by the importance of patent protection for the location decision.

<h>CONCLUSION</h>
----------

This paper aimed at investigating the extent to which product and labour market
regulations affect, among other socio-economic factors, the probability that top corporate
research and development (R&D) investors locate in a particular country. Our results show
that PMR and EPL exert a mutually reinforcing negative effect on the location of top R&D
investors’ subsidiaries. Moreover, of the three components of the PMR indicator — barriers
to trade and investment, state control and barriers to entrepreneurship — the first is the
one with the highest negative marginal effect. Finally, a caveat should be kept in mind
when reading our results. In our analysis we consider a particular set of firms (top R&D
investors worldwide) and their current subsidiaries, for which we don’t have the year of
establishment. This focuses our analysis on the observation of conditional ex-post
probabilities, and not on the genesis of the multinational foreign subsidiaries network
(Egger et al., 2014). Second, the aforementioned PMR/EPL mutually reinforcing effect does
not automatically imply that markets should be deregulated as such because, as shown in
Aghion et al. (2005) for innovation, an excessive reduction of market regulation could
even negatively influence country attractiveness. Therefore, further research on this area
may provide additional insights on the necessity to carefully consider how PMR and
employment protection interact in different socio-economic environments taking into
account the multiple effects they have on the society.


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<ART>Simulated economic impacts in applied trade modelling: A comparison of tariff aggregation approaches
================================================================================

Authors: Mihaly Himics, Giulia Listorti, Axel Tonini
DOI: 10.1016/j.econmod.2019.08.007
Year: 2020  |  Pages: 344-357
ASJC codes: 2002
Keywords: Aggregation bias, Quota rent, Tariff aggregation, Tariff rate quotas, Trade policy simulation

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper assesses the performance of two recently developed tariff aggregators in reducing tariff aggregation bias by analysing Swiss beef market liberalisation scenarios. Specific relevant sources of bias are addressed: substitution effects on import demand, Tariff Rate Quotas and overprotection in tariffs. The aggregators are linked to a global large-scale partial equilibrium model and benchmarked against a standard aggregator. The choice of the aggregation method shows considerable effects on simulated economic impacts, specifically if the dispersion in tariffs or tariff cuts is large. A large bias is revealed in simulated gains from trade liberalisation using the standard aggregator. The impacts on traded quantities are found to be overestimated, while price and welfare effects can be higher or lower by switching to alternative aggregation methods. By reducing aggregation bias and depicting negotiated tariff schedules more directly, the proposed aggregators enhance the contribution of trade modelling to evidence-based policy making.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Market access policies, and import tariffs in particular, are typically defined at the
detailed tariff line level.3 The “tariff schedule” of a country normally includes
thousands of tariff lines, and trade statistics are also often recorded at this fine level
of disaggregation.4 As trade negotiation offers and requests made in trade talks (tariff
cuts, exceptions to tariff cuts, sensitive products etc.) usually refer to tariff lines,
economists need to analyse and process tariff distributions and detailed trade data when
they support negotiators by providing simulated potential economic impacts of policy
options. However, most applied models of international trade operate by using more
aggregated commodities, each of them often covering a wide array of tariff lines. As a
result, detailed tariff line level data first needs to be aggregated, which in turn leads
to aggregation bias in simulated model outcomes as well as to partial loss of information
on detailed trade and trade policy patterns. In this paper we assess the performance in
reducing tariff aggregation bias of two recently developed tariff aggregators. The focus
is on three specific sources of bias which are relevant to a wide range of agri-food
markets and empirical applications: substitution effects on import demand, Tariff Rate
Quotas (TRQ) and existing overprotective buffers of tariff protection. The proposed
approaches depart from state-of-the-art consistent tariff aggregation techniques. The
first one, the trade expenditure aggregator (TE), is an equivalence measure of tariff
protection, defined as the uniform tariff rate that is equivalent to a set of individual
tariffs in terms of its impact on trade expenditures. The second one, the Tariff Reduction
Impact Model for Agriculture (TRIMAG) aggregator, adjusts aggregation weights based on a
CES function defined at the tariff line level, and provides an explicit representation of
the overprotective part of the duties. The proposed aggregators are linked to a global
large scale partial equilibrium model as standalone modules, thereby demonstrating an
impact assessment approach that can be replicated to a wide array of trade modelling
applications. This paper provides a concrete application of the proposed impact assessment
approach by examining a set of Swiss beef market liberalisation scenarios. Simulation
results are also benchmarked against a standard aggregator for systematic comparison. Our
assessment shows that the choice of the aggregation method has considerable effects on
simulated economic impacts, specifically in the case of heterogeneous tariff cuts and
large tariff dispersion. Simulation results also suggest that the proposed aggregators
reduce aggregation bias. A further advantage of the proposed tariff aggregators is that
they allow for a more accurate implementation of negotiated tariff schedules in applied
equilibrium models, by exploiting tariff line level details of trade- and trade policy
data. Against this background, we argue that the proposed aggregators enhance the
potential contributions of trade modelling to evidence based policy making. The paper is
structured as follows. In Section, 2, we discuss possible sources of tariff aggregation
bias and its measurement (Section 2.1), and then formally introduce our strategy for
consistent tariff aggregation (Section 2.2), presenting in detail the TE and TRIMAG
aggregators (Section 2.3 and 2.4, respectively). Then, in Section 3 we briefly describe
the CAPRI model. After that, in Section 4 we define the application to the Swiss beef
market as well as the test tariff dismantling scenarios. Data and simulation results are
presented and discussed in Section 5. Finally, concluding remarks are reported in Section
6.

<h>ADDRESSING TARIFF AGGREGATION BIASES</h>
------------------------------------

This section presents a comprehensive yet concise review of the most relevant sources and
measurement issues related to tariff aggregation bias (Section 2.1), followed by the
presentation of our approach (Section 2.2) and of the proposed tariff aggregators
(Sections 2.3 and 2.4, respectively).

<hs>  Sources and measurement of aggregation bias</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The straightforward way to improve exploitation of existing datasets at the tariff line
level is to extend trade models to the tariff line. Indeed, there have been several
attempts in this direction in the literature. Grant et al. (2007) iteratively link a
Computable General Equilibrium (CGE) model with a satellite partial equilibrium (PE) model
for dairy products at the HS 6 level. Narayan et al. (2010) opt for a nested general
equilibrium (GE)/PE modelling approach in order to use tariff line level data to assess
the impact of tariff liberalisation on the Indian auto industry. Britz and van der
Mensbrugghe (2016) advocate advanced database filtering methods and algorithmic
improvements to increase regional and commodity-wise disaggregation in trade models and
therefore limit the need for aggregation at the same time. However, these approaches still
only offer partial solutions because they only cover selected sectors or they still do not
disaggregate models to the tariff lines. Therefore, computational and data issues still
seem to force applied economists to keep to more aggregated commodity and regional groups
in applied trade modelling. Global statistics on both demand and supply are still lacking
at the tariff line level, and when extending import demand systems to the tariff line, the
number of possible bilateral trade flows quickly becomes computationally unmanageable.
Practitioners are consequently confronted with the choice of a tariff aggregation method
that fits both the technical implementation and structure of their modelling tools as well
as the focus of the specific policy question to be addressed. Aggregation over tariff
lines inevitably leads to biases in simulated impacts of trade liberalisation, at least
for some model outcomes. Measuring this bias involves comparing the simulated results
derived using both a disaggregated (tariff line level) and an aggregated version of the
same model. However, impacts simulated using the disaggregated model cannot be considered
to be ‘true’ impacts because they are determined by the model parameterization (Pelikan
and Brockmeier, 2008b). Therefore, the lack of a clear reference point does not allow for
an absolute measurement of the bias, but instead all measures of the aggregation bias are
necessarily relative to a selected disaggregated model structure and its parameterization.
Empirical evidence still suggests that the aggregation bias is substantial. Laborde et al.
(2017) compare simulated impacts of global trade liberalisation using different tariff
aggregation methods in the LINKAGE model (Van der Mensbrugghe, 2005) and find that the
optimal tariff combination of Anderson (2009), which we also discuss below, almost double
welfare impacts compared to traditional trade weighted aggregators. The simulated terms-
of-trade and real income effects largely vary between regions, and is generally largest
for developing countries. They also find a crucial impact of model parameterization on the
aggregation bias: increasing substitution elasticities in their modelling framework leads
to larger differences in simulated welfare gains. In a modelling exercise with using trade
restrictiveness indices (Anderson and Neary, 2005) in the GTAP model (Hertel, 2007),
Pelikan and Brockmeier (2008a) also find that standard trade weighted tariff aggregation
leads to largely underestimated welfare gains from global trade liberalisation. However,
the trade modelling literature in general (including gravity models) is inconclusive about
the relative empirical size and even about the direction of the aggregation bias. While
some such as French (2016), who find a downward bias in a flexible model allowing for
comparative advantage across products for every country, Bektasoglu et al., 2017 calculate
an upward bias in estimating non-tariff measures using traditional gravity modelling
techniques. Regarding the main sources of the aggregation bias, the trade protection
measurement literature attributes them either to (i) the conversion of different types of
tariffs (ad valorem, specific, and compound) to a common metric; or (ii) to the
aggregation process from the tariff line to a more aggregated commodity level (Pelikan and
Brockmeier, 2008a).5 With regard to the aggregation process, standard methods only use
trade data for defining aggregation weights. In principle, other supply and demand related
data (e.g. production and consumption) are also relevant for tariff aggregation, but are
often neglected due to data availability. For example, the estimation of product-
substitution in the consumption bundle requires observed consumption patterns at the
tariff line level. Many ways of averaging tariffs for trade modelling can be observed in
the literature. Tariffs might receive the same weight when calculating a simple average;
medians can be used to take skewed tariff distributions into account; or weighted averages
can be formed by applying, for example, import shares valued at border prices as
aggregation weights. The latter approach is specifically prone to endogeneity bias since
highly taxed goods tend not to be imported and so might even receive zero weights.
Therefore, trade weighted average tariffs typically underestimate trade restrictiveness.
They not only tend to smooth out tariff peaks but they also tend to underestimate
simulated welfare gains from trade liberalisation (see Martin et al., 2003). Specific
weighting schemes are readily available to reduce the endogeneity bias, e.g., the
“reference group” method (Bouet et al., 2008; Guimbard et al., 2012) which clusters
countries into groups of similar GDP per capita and trade openness indices. Bach and
Martin (2001) proposed and Anderson (2009) fine-tuned an approach for eliminating all
aggregation bias in the GE framework for a selected model outcome. Their welfare
consistent aggregation corrects the entire aggregation bias for simulated welfare impacts
by introducing an optimal combination of tariff aggregators in a modified balance of trade
condition into GE models. Restrictions for the consistency include imposing separability
conditions for consumer utility maximisation and assuming zero price impact on the
domestically produced good. While the first assumption is commonly present in most CGE
models through the Armington assumption, the latter is quite restrictive, and it has not
been possible to significantly relax it even in recent extensions of the approach for
large-scale CGEs (Laborde et al., 2017). The approach also requires the parameterization
of complete supply and demand systems against a large number of behavioral parameters,
such as substitution elasticities. This paper does not aim at a comprehensive
classification of the possible sources of tariff aggregation bias. Instead, the focus is
on three specific sources: (i) demand-side substitution effect observed at the tariff line
level; (ii) the endogenous determination of tariffs under Tariff Rate Quotas (TRQ); and
(iii) the difference between initial unit quota rents and applied out-of-quota tariffs
under binding TRQs, potentially increased with “water” in tariffs. The latter source of
bias is treated in the following discussion as an over-protective part of the duty. The
above sources of aggregation bias are not only relevant to our empirical investigation of
the Swiss beef market liberalisation, but they are also relevant to a wider range of
policy applications. Firstly, the substitution effect-related aggregation bias is closely
linked to the heterogeneity of commodity groups. Trade liberalisation can change the
composition of the consumed commodity group significantly. Assuming separable homothetic
preferences, as is often the case in trade models, this demand side adjustment is
attributed to relative price changes within a larger product group. When facing large
tariff dispersion (either due to differences in initial tariff rates or due to different
tariff cuts), significant changes in relative import shares can be expected and so the fix
trade shares assumption underlying standard tariff aggregation becomes too restrictive.
Consistent aggregation (Anderson, 2009; Himics and Britz, 2016) offers an approach for
correcting the demand side adjustments by setting up an explicit import demand system at
the tariff line. This approach is also followed in this paper and Constant Elasticity of
Substitution (CES) type utility aggregators at the tariff line are set up to either (i)
adjust aggregation weights according to shifts in import shares; (ii) or to calculate an
equivalent average tariff in terms of shifts in trade expenditure shares. The point of
departure from the literature is that the authors of this paper do not aim at full
consistency in terms of a single selected model outcome (e.g. welfare), but rather the
applicability of the proposed aggregators in reducing the substitution effect-related bias
in a range of simulated outcomes is tested. Secondly, covering TRQ related aggregation
bias is crucial for the liberalisation of global agri-food markets, which are often
regulated by complex TRQ systems (de Gorter and Kliauga, 2006; WTO, 2012). Opening TRQ-
regulated market access (e.g. in the form of expanding quota limits and lowering in- or
out-of-quota tariff rates) has been included in many recent trade negotiations, including
the EU-Mercosur (Ramos et al., 2010) talks and also the current debate on post-Brexit
trade relations of the EU, and the UK with third countries (Revell, 2017). TRQs are two-
level tariffs with a limited volume of imports permitted at the lower “in-quota” tariff
and all subsequent imports charged the higher “out-of-quota” tariff. In other words, the
tariff rate applied on imports depends on the quota fill rate. Standard aggregation
techniques do not always take the possibility of a TRQ regime shift into account (e.g.,
from an in-quota to an out-of-quota situation), and neither the induced adjustment in the
applied tariff rates, or at least not at the tariff line level where TRQ thresholds are
usually defined.6 Neglecting TRQ regime shifts in standard tariff aggregation (e.g., by
converting TRQs into an equivalent tariff rate, additional trade cost or price gap), can
lead to both over and underestimation of the applied tariff rate. The literature is
inconclusive regarding the size of the potential aggregation bias from TRQ regime shifts.
Using aggregated TRQ data in the MIRAGE CGE model, Decreaux and Ramos (2007) find that the
aggregation bias itself is relatively small compared to the bias induced by not modelling
the TRQ regime shifts explicitly in the aggregated (CGE) model. On the other hand, Himics
and Britz (2016) found that the aggregation bias can be significantly large when using fix
aggregation weights, even for scenarios involving moderate TRQ expansion. In order to
capture the interplay of tariff rates and imported volumes under a TRQ regime, we follow
different approaches in the two aggregators we propose. One of the aggregators replicates
the Mixed Complementarity Problem (MCP) formulation of Himics and Britz (2016) for
modelling TRQ regime shifts at the tariff line, while the other one aggregates in-quota
and out-of-quota rates separately, and leaves the explicit TRQ modelling for the
aggregated equilibrium model at hand, similar to Decreaux and Ramos (2007). A significant
impact of tariff “water” or “binding overhang”, which is defined as the gap between bound
and applied rates (Bchir et al., 2006), on simulated gains from trade liberalisation has
long been identified in the literature (e.g. Beshkar et al., 2015). The gap between
applied and bound rates also adds another source of complication to TRQ modelling, further
motivating the research presented in this paper in this direction. The “water” in tariffs
provides trade negotiators with a leverage to offer tariff cuts that have no significant
impact on domestic prices (and therefore domestic producers) in the short term (Bchir et
al., 2006). Not only the “water” in tariffs, but also the difference between unit quota
rent and the out-of-quota rate provides negotiators with an additional buffer to accept a
decrease in applied rates as the decrease will not necessarily affect import prices. To
illustrate this point, consider a binding TRQ (Fig. 1) in the small country case. The
equilibrium price is determined as the intersection (A) of the net import demand and
excess supply curves, the latter being fully determined by the quota threshold and the TRQ
tariff rates (see Skully, 2001). In case the TRQ is binding, net import demand is strong
enough to induce imports up to the TRQ limit but fails to trigger imports beyond the
threshold. Consequently, an economic (quota) rent is generated. Tariff cut scenarios would
only have an impact on imports, ceteris paribus, if the out of quota rate is reduced
beyond the per unit quota rent. In other words, as long as the applied rate after tariff
cuts stays above the unit quota rent, import demand will not exceed the quota level and
thus no price impact will be triggered. In order to highlight this additional buffer for
trade negotiators to decrease tariffs without an impact on imports, the sum of the “water”
or “binding overhang” in tariffs and the gap between unit quota rent and applied rates is
denoted as the overprotective part of the tariff. Finally, the overprotective part of the
tariff (partly defined by the size of the quota rent) is the third source of aggregation
bias specifically examined in this paper. Lips and Rieder (2005) identified that standard
tariff aggregation yields biased aggregate quota rents, and proposed using aggregation
weights based on quota rents and tariff revenues. They find significantly smaller price
impacts in a TRQ expansion scenario using the Global Trade Analysis Project (GTAP) model
when quota rents are taken into account although the initial unit quota rents in their
study are based on simplified assumptions rather than on real data. Himics and Britz
(2016) also highlight the impact of quota rent assumptions on simulated results when
showing that setting quota rents uniformly at half of the difference between in- and out-
of-quota rates largely overestimates effective tariff reduction. A data driven approach is
also implemented in this paper to specifically define the unit quota rent and therefore
decrease the potential aggregation bias from arbitrarily setting initial quota rents.
Quota rents for estimating trade liberalisation impacts are not only relevant for
negotiators, but farmers might also perceive potentially decreasing economic rents as a
policy risk (Nogueira et al., 2012).

<hs>  The proposed tariff aggregators</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Two strategies to go beyond standard tariff aggregation and address the above sources of
aggregation bias are proposed. Firstly, the method presented in this paper departs from
state-of-the-art consistent tariff aggregation techniques and sacrifices full consistency
for the sake of improving a multitude of simulated model outcomes. The trade expenditure
aggregator (TE), evaluated here is an equivalence measure of tariff protection, defined as
the uniform tariff rate that is equivalent to a set of individual tariffs in terms of its
impact on trade expenditures. Formally, the TE aggregator is part of the optimal tariff
combination of Himics and Britz (2016), originally developed for flexible welfare
consistent aggregation over exporter countries. The TE aggregator includes an import
demand system at the tariff line level, driving the simulated changes in the composition
of commodity groups and the related trade expenditures. As proposed here, the TE
aggregator also includes explicit TRQ functions at the tariff line level to take into
account the adjustments in applied tariff rates under TRQ. The TE aggregator therefore
directly addresses two of the investigated sources of aggregation bias: (i) changes in the
composition of the imported consumption bundle; and (ii) TRQ regime shifts. With regard to
the over protective part of the duty, the TE aggregator takes the tariff “water” into
account but sets the initial quota rent on the basis of ad-hoc rules (arbitrarily). The
strategy in the second approach adopted in this paper is to include some of the
methodological elements of the consistent aggregation into weighted average tariff
calculations. Aggregation weights are adjusted to the changes in consumption shares within
a commodity group. The proposed Tariff Reduction Impact Model for Agriculture (TRIMAG)
aggregator adjusts aggregation weights based on a CES aggregator function, defined at the
tariff line level. TRIMAG also explicitly takes into account the overprotective part of
the duty by calculating the price impacts of tariff cuts at the tariff line level. A price
transmission function in TRIMAG calculates import price changes, taking into account the
initial overprotective part of the duties estimated from a Switzerland-specific database
of wholesale domestic prices and CIF prices at the HS 8 level (Listorti et al., 2013).
Consequently, TRIMAG addresses the aggregation bias stemming from both substitution
effects and from TRQ regime switches. Furthermore, in the case of binding TRQs, the above
domestic price database enables TRIMAG implementing a data driven approach to estimate the
overprotective part of the duty and take this into account in the price transmission from
tariff cuts to domestic import prices. Both the TE and the TRIMAG aggregators neglect the
income effect of tariff revenues that might accrue to consumers. The assumption of
ignoring tariff revenues does not seem to be too restrictive in the PE framework of this
paper, and, more generally, if tariff revenues has little impact on consumer income.7 In
addition, both aggregators are built for the small country case and assume completely
elastic excess supply from the rest of the world, at the tariff line level (see section
3.2). Following a standard assumption of the consistent aggregation literature, prices of
domestically produced and imported goods are independent, simplifying the consumers’
utility maximisation (expenditure minimisation) problem for finding an optimal consumption
bundle after trade liberalisation. The features of the proposed aggregators, including a
traditional fixed weight aggregator for comparison, are summarised in Table 1. The two
aggregators proposed were tested by analysing alternative Swiss tariff dismantling
scenarios for beef imports, following a typical two-stage approach (Francois et al., 2005;
Philippidis and Sanjuán, 2007; Egger et al., 2015 to name a few). First aggregated ad
valorem equivalent (AVE) tariff rates were estimated using disaggregated data at the
tariff line level. Second, the overall impact on agricultural markets was analysed by
plugging in the estimated AVEs in a PE model working at a more aggregated level (e.g.
commodity level). More precisely, the TE and TRIMAG aggregators, and additionally a
traditional fixed weight aggregator for comparison, provide a set of aggregated AVE tariff
rates for the Common Agricultural Policy Regionalised Impact (CAPRI) model (e.g. Britz and
Witzke, 2014) before and after trade liberalisation, making a systematic and direct
comparison of the approaches possible. In the first stage, aggregated tariffs are
calculated using the different methods, which then enter the calibration process of CAPRI
in the first step. The outcome of the first stage is the set of three reference scenarios
(one corresponding to each aggregation method). The assumed tariff cuts are applied in the
second stage, where the liberalised tariff schedule is used to calculate aggregate tariffs
again post-liberalisation. The aggregated tariffs are transferred into CAPRI to simulate
trade (market balances and prices) and welfare impacts for the trade dismantling
scenarios. The trade expenditure (TE) tariff aggregator and the TRIMAG tariff aggregator
are discussed in detail in the following Sections 2.3 and 2.4, respectively.

<hs>  The trade expenditure (TE) tariff aggregator</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

With respect to the link to the CAPRI model, the aggregate (importer-specific) tariff
rates of equation (6) are implemented in CAPRI as AVE tariff rates. As a result, the
endogenous modelling of the TRQ system in the TE aggregator is shifted from CAPRI to a
standalone aggregation module. Shifting policy representations out of the core
(aggregated) model has various numerical advantages as the number of equations decreases.
On the other hand, removing the (beef) TRQ function from CAPRI breaks the link between
aggregated quota thresholds and tariff rates, possibly altering simulated trade impacts.

<hs>  The TRIMAG tariff aggregator</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The TRIMAG model, developed by the Swiss Federal Office for Agriculture (FOAG) (Listorti
et al., 2013), calculates aggregate tariffs based on current tariff data (reference mode)
as well as considers possible tariff cut scenarios (simulation mode). A particularity of
the Swiss tariff schedule is that in- and out-of-quota tariff rates of the same TRQ are
registered under different tariff lines.8 Following this separation of tariff rates,
TRIMAG calculates aggregate in- and out-of-quota rates separately. Tariff rates are also
differentiated by the geographical region of origin (EU and rest of the world RW9). The
following sections provide more methodological detail on the reference and simulation
modes.

     <hss>The reference mode</hss>

        TRIMAG combines three weighting methods in the reference mode to reduce the
        endogeneity bias related to small traded volumes of highly protected tariff lines
        (see discussion in Section 1): (i) bilateral import weighted average, which gives
        a large weight to the most important trading partners; (ii) total imports weighted
        average, which puts the largest weights on tariff lines with the largest import
        demand within the aggregated commodity groups; (iii) a simple arithmetic average,
        which is not affected by traded volumes and is therefore free from the endogeneity
        bias.

     <hss>The simulation mode</hss>

        In simulation mode, TRIMAG updates the aggregation weights according to the
        assumed change in the current tariff schedule. Unlike the linear aggregation in
        equation (17), the updated weights enter a CES-type tariff aggregator, which
        calculates the modified aggregate tariffs. Once the updated import prices at the
        8-digits level have been determined, they enter a CES utility aggregator, which
        drives substitution within the consumption bundle, corresponding to a standard
        consumer expenditure minimisation framework under fix utility assumption.
        Consequently, the adjustment in the consumption mix is triggered by relative price
        changes at the tariff line level. The adjustment in the consumption mix (i.e.
        substitution effect) is therefore driven by the equation system (19)–(21). Note
        that a demand system has not been formally defined at the tariff line, as it is in
        consistent aggregation, but only adjust aggregation weights depending on a CES-
        type aggregator.15 Instead of using CES share equations and the associated
        composite price indexes as is typical e.g., in the CGE modelling literature, a
        theoretically equivalent formulation based on a numeraire tariff line was used in
        this paper. The price transmission function in equation (18) follows a standard
        price gap approach based on fix world (CIF) prices, but takes a possible
        overprotective part in the duties under binding TRQs into account. Tariff cuts are
        only transmitted to the import prices if the overprotective part under TRQs has
        been eroded. However, possible pricing behaviour of exporting firms is not
        considered in the analysis. Exporting firms might pass through tariff rate changes
        to the import markets to varying extent, adjusting their mark-ups and pricing
        their exported goods depending on the tariff protection of the export destination
        (e.g., see Mallick and Marques, 2008, 2012). The aggregated in- and out-of-quota
        tariff rates in the empirical application below are transferred directly16 to the
        CAPRI model, and there they are used to parameterize the beef TRQ equations.

<h>SHORT DESCRIPTION OF THE CAPRI MODELLING SYSTEM</h>
-----------------------------------------------

The following section provides a short description of the CAPRI modelling system used for
the scenario analysis of the beef tariff dismantling scenarios. The focus is only on those
aspects of CAPRI that are relevant for the simulation exercise presented in this paper. A
more detailed description can be found e.g. in Britz and Witzke (2014). CAPRI is a global
comparative-static deterministic partial equilibrium model with a focus on European
agriculture. Nevertheless, CAPRI includes a global market module covering the main
agricultural and food commodities. The market module covers 77 countries or country
aggregates in 40 trade blocks and about 50 products. The model follows the Armington
approach for simulating bilateral trade flows, taking into account the price impacts of
bilateral and multilateral trade policy instruments (including ad valorem and specific
tariffs and tariff-rate quotas). The market model consists of structurally identical
template equations for all regions and commodities. Regional and commodity-wise
specificities are expressed by the differences in parameterization. Supply and demand
equations are consistent with microeconomic theory by imposing homogeneity and other
curvature conditions during calibration. The supply of agricultural and feed compound
sector are derived from a Normalized Quadratic profit function while final demand is based
on Generalized Leontief demand systems (Diewert, 1971). For Switzerland, in order to
improve the empirical foundation of the supply response, the supply elasticities are based
on estimates derived through sensitivity analyses carried out using the SWISSland agent
based model (Möhring A. et al., 2016). The CAPRI model outputs comprises several economic
indicators which include welfare figures based on a partial equilibrium setting for
ceteris paribus conditions for the sectors outside agriculture. The CAPRI model has been
applied for trade-related policy impact analysis in the literature (e.g. Burrell et al.,
2011; Burrell et al., 2014; Pelikan et al., 2015). However, for the sake of this study,
CAPRI was extended with tariff aggregation modules17 calculating aggregate tariffs for
CAPRI in both calibration and simulation. In the case of the TE and fixed weight
aggregators the model-endogenous TRQ instrument also had to be shifted from CAPRI to the
standalone aggregation modules.

<h>SCENARIO DEFINITION</h>
-------------------

Beef production represents slightly more than a quarter of the total Swiss agricultural
production in value terms (BLW, 2017). A self-sufficiency rate of around 80% renders
Switzerland a net importer. Meat markets are regulated by a multilateral TRQ system with a
large number of sub-quotas for specific commodities (Loi et al., 2016). The multilateral
TRQ for red meats includes 22 in-quota and 23 out-of-quota sub-quota tariff lines18 for
beef products. The TRQ covers a very heterogeneous product group ranging from live animals
to fresh or frozen carcasses, fresh or frozen meat with bones in or boneless, and offal,
with a total notified volume of 22,500 tonnes. Out-of-quota quota tariffs are often
prohibitively high, and therefore imports mostly occur within the quota limit.19 See also
Loi et al. (2016) for more details. The proposed tariff aggregation methodologies were
implemented at the 8-digits level, therefore taking advantage of all of the detail in the
Swiss tariff schedule, which is also defined at that level of detail. Although Swiss beef
TRQs are normally totally filled, assumptions on the initial unit quota rents still need
to be made. Theoretically, the unit quota rent can be set to anything between the in- and
out-of-quota rates in a binding TRQ regime (Skully, 2001). The TRQ functions of the TE
aggregator are built on complementarity slackness conditions mimicking potential TRQ
regime shifts at the tariff line level. The calibration of the system still requires an
assumption on the initial quota rents, as initial import prices faced by consumers include
the quota rent. Initial unit quota rents for the TE aggregator are uniformly set to the
maximum for all tariff lines, reflecting a generally strong Swiss import demand for beef
commodities. On the other hand, TRIMAG follows a data-driven approach and calculates
initial unit quota rents as the difference between wholesale domestic and the
corresponding CIF prices (plus in-quota tariff if applicable). Traditional fixed weight
aggregate tariffs are also calculated for comparison. More precisely, an import weighted
aggregator that is quite standard in the literature was selected in this paper. This
follows the approach of Bouet et al. (2008) in calculating applied tariff rates under TRQ:
(i) if the fill rate is between 95% and 99%, the applied rate is an arithmetic average of
the in-quota and out-of-quota rates; (ii) if the fill rate is below 95%, the in-quota rate
is taken; and (iii) above a 99% fill rate, the out-of-quota rate is calculated. To avoid
mixed impacts which would complicate a systematic comparison of simulated results, the
tariff dismantling scenarios presented in this paper are designed to be simple. Two
liberalisation scenarios are implemented. All bound rates for Swiss beef imports from the
EU in the homogeneous cuts scenario are cut by 50% at the 8-digits HS level. More
heterogeneity regarding the tariff cuts is introduced in the second (heterogeneous cuts)
scenario by making two tariff lines (0201.3099, fresh boneless beef meat, and 0202.3099,
frozen boneless beef meat) exempt from the general 50% tariff cuts. Although the two
exempted tariff lines are characterized by similar tariff protection, they have
significantly different aggregation weights in the reference scenario, and the
overprotective part in the duties varies considerably. The heterogeneity in tariff rates
and tariff cuts as well as the presence of significant overprotection in tariffs makes
these scenarios particularly useful in evaluating the different tariff aggregators. In
fact, it is expected that the three aggregation biases discussed in this paper will be
relevant to the scenarios by design. Firstly, initial aggregation weights for a product
group are not uniformly distributed, and so the cuts on the tariff lines have different
impact on the aggregate tariff after liberalisation. The heterogeneity in initial import
prices induces significant substitution effects, including in the case of uniform tariff
cuts, as relative price changes after liberalisation might differ substantially. Making
the tariff cuts heterogeneous may further increase this substitution effect. Secondly,
explicitly considering TRQ regime shifts at the tariff line is expected to provide more
precise aggregate tariff cuts. The increased precision was assessed by comparing the
calculated aggregated tariff cuts across the aggregation approaches. As an additional
methodological difference, TRIMAG calculates aggregated in- and out-of-quota rates, and
does not convert the whole TRQ mechanism into an equivalent tariff rate as the other two
aggregators do. Therefore, using TRIMAG aggregated tariffs means the aggregated (beef) TRQ
function in CAPRI can be taken advantage of. Comparing TRIMAG simulated results to the
other two aggregators therefore provides an estimate of the bias that might be introduced
by substituting the TRQ mechanism with a simple equivalent tariff rate. Finally, comparing
TE and TRIMAG results sheds light on the importance of estimating the overprotective part
in the duties using domestic price data.

<h>DATA AND SIMULATION RESULTS</h>
---------------------------

In this section both the input data used for the modelling exercise are presented and the
simulation results derived with the three tariff aggregators are systematically compared.

<hs>  Data base construction</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

Import values and quantities from the Swiss-Impex database (Swiss-Impex, 2015) were used
for the TE tariff aggregator. The data were extracted at 8-digits level and averaged over
the years 2009–2014. Exporter countries are mapped and potentially aggregated to the CAPRI
regions before setting up the demand system of the TE aggregator, so the exporter-specific
aggregate tariffs of equation (6) can be plugged into CAPRI directly. In-quota and out-of-
quota tariffs in the Swiss tariff schedule are registered under different tariff lines. In
order to calibrate the TRQ functions of the equation system (9)–(12), all out-of-quota
tariff lines had to be paired with their corresponding in-quota tariff lines. Therefore,
the TE aggregator covers 22 (merged) TRQs for Swiss beef imports. The standard (fixed
weight) aggregated tariffs are calculated based on the same Swiss-Impex data and the same
merged TRQ system. The TRIMAG aggregator has its own trade and tariff database at the
8-digit level, with a base year defined as an average of the 2004-09 in the case presented
in this paper. The TRIMAG database includes bound and applied tariffs, imports values and
quantities, as well as CIF prices for the main trading partners20 and domestic wholesale
Swiss prices.21 Beef related TRIMAG data used in this analysis are illustrated in Table 2.

<hs>  Tariff cut calculations (stage one)</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In the first stage of the modelling exercise, the aggregate beef tariff cuts are
calculated according to the three tariff aggregation methods, each of them implemented as
pre-model aggregation module to CAPRI. Differences in calculated aggregate tariffs are
already present in the corresponding reference scenarios (Table 3). TRIMAG calculates an
aggregated in-quota rate of 15% and an aggregated out-of-quota rate of 145%. The 142% AVE
in Table 3 is the marginal tariff rate that the aggregated beef commodity in CAPRI is
calibrated to. The large AVE, close to the out-of-quota rate, implies a strong import
demand and a high unit quota rent respectively in the reference scenario. The TE
aggregator calculates a significantly lower (83%) aggregate AVE rate for imports from the
EU. The AVE for beef calculated with the fixed weight aggregator is between the other two
aggregation approaches (99%). Most TRQs at the tariff line level are close to the 100%
fill rate, and so the fixed weight aggregator sets the unit quota rent under these TRQs at
exactly the midpoint between in- and out-of-quota rates during the tariff aggregation.
Using fixed aggregation weights in the homogeneous cuts scenario, a −50% uniform tariff
cut on all tariff lines simply translates to a −50% aggregated tariff cut. By allowing
aggregation weights to change, the aggregate tariff cut on EU imports departs from the
−50% middle value, and respectively becomes −48% and −51% for the TE and TRIMAG
aggregators in the homogenous scenario. The similar estimates suggest only marginal
relative price changes and so only small adjustments in the consumption mix due to
substitution effects in the case of uniform tariff cuts. However, introducing
heterogeneity by making two important tariff lines exempt from tariff cuts (heterogeneous
cut scenario) opens the gap between estimated aggregate tariff cuts. Here, larger relative
price changes induce more adjustments in the consumption mix toward commodities with
higher initial tariffs. The aggregate tariff cut therefore becomes relatively smaller when
calculated with tariff aggregators that take the substitution at the tariff line into
account. The explicit TRQ modelling in the TE aggregator adjust applied tariff rates under
TRQ upwards as imports reach the quota threshold. This upward adjustment increases the
aggregate tariff rate in the scenarios, further decreasing the aggregate tariff cut
compared to standard approaches. Accordingly, aggregate cuts in the heterogeneous cuts
scenario are significantly smaller using the TE and TRIMAG approaches. In the TE
aggregator, the average tariff cut is only −18% for the EU. Even though the consumption
shares of the exempted tariff lines decrease, their initially high relative shares and
large initial tariff rates keep the average tariff at a higher level than in the
homogeneous cuts scenario. The relative average tariff cut calculated by TRIMAG (−39%) is
also lower compared to the fixed weight aggregator, again mainly due to the large initial
tariffs and trade shares of the exempted tariff lines. The marginal tariff rates reported
for TRIMAG in Table 3 coincide with the out-of-quota tariff rates in both scenarios as the
increasing imports push the TRQ regime to the out-of-quota situation. Regarding the
exempted tariff lines, one of them has a large aggregation weight and therefore reduces
the average tariff cut substantially, while the other tariff line has a much lower weight
and so has almost no impact on the aggregated cuts (Fig. 2). It is important to note here
that such a difference in tariff cuts between the homogeneous and heterogeneous tariff cut
scenarios is not found for the fixed weight aggregator. Aggregation weights do not change
for the two exempted tariff lines, limiting the impact on the aggregated tariff cut
compared to aggregation techniques explicitly addressing the substitution effect (−46%).

<hs>  CAPRI simulation results (stage two)</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In the second stage of the modelling exercise, the average beef tariff cuts are introduced
in CAPRI, and the respective comparative static simulations are performed. The smaller
aggregate tariff cuts of the first stage induce smaller simulated trade impacts in CAPRI
in the second stage for the TE and TRIMAG aggregators, specifically in the heterogeneous
cuts scenario. According to the TE aggregator the EU (dominating Swiss beef imports)
countries increase their exports by 65% in the homogeneous and by 22% in the heterogeneous
cuts scenario results whereas using TRIMAG an increase of 64% and 45% respectively was
simulated (Table 4). In contrast, the fixed weight aggregator only delivers marginal
differences in simulated trade impacts between the two scenarios (70% and 63%). The larger
import price effects of TRIMAG in the second stage are largely due to the explicit beef
TRQ functions in CAPRI, which allow for a more flexible price adjustment compared to the
ad valorem representation of TRQs used by the TE and standard aggregators. Firstly, traded
quantities are too small to have significant impact on the beef market prices at the
source of origin, therefore import price effects are mostly defined by changes in the
applied tariff rates. Applied tariff rates, on the other hand, tend to drop more in trade
liberalisation scenarios using explicit TRQ functions, because the applied rate may settle
in the new equilibrium between the in- and out-of-quota tariff rates. Secondly, non-EU
import prices only decrease for TRIMAG, with an additional negative impact on the average
beef import price. The impact on import prices from non-EU countries is due to the
explicit TRQ functions on these bilateral trade links (Brazil, Argentina and USA all take
advantage of a multilateral beef TRQ). As demand for non-EU beef in Switzerland is
decreasing, the unit quota rents (and therefore the shadow prices) for imports from non-EU
countries decrease as well. Regarding the different import price impacts calculated with
the fixed weight and TE aggregators (ad valorem representation of TRQs in both cases), the
effects closely follow the relative differences in tariff cuts of stage one (−23% and −19%
decrease in the average import price in the homogeneous scenario, respectively). As
observed for the tariff cuts above, the heterogeneous cuts scenario results in smaller
impacts also on import prices, for all three aggregation methods. Average import prices
decrease by −20% for the fixed weight aggregator, −7% for the TE aggregator, and −23% for
TRIMAG. The above import price changes are transmitted to the producer prices in CAPRI,
taking into account both the substitution of domestically produced goods with imported
ones as well as the substitution of imported goods from different origin in the
consumption bundle. Consistently to the effects on average import prices, simulated
impacts on producer prices are the largest for the TRIMAG approach (Fig. 3). In the
homogenous tariff cuts scenario a −29% decrease in the average beef import price induces a
−16% reduction in the domestic producer price with the TRIMAG approach. The price
transmission is similar in relative terms for the other two aggregators as well: from a
−19% change in the import price into a −9% decrease in the producer price for the TE
aggregator; and from a −23% to a −12% decrease for the standard aggregator. The adjustment
in Swiss beef supply in CAPRI is driven by the respective supply elasticities, empirically
estimated using the SWISSland agent based model (Möhring A. et al., 2016). The supply
response for most agricultural products is inelastic in the medium run (including beef),
causing beef supply to decrease less than proportionally to simulated producer price
changes. Producer price and production impacts are, in general, smaller in the
heterogeneous scenario. At the same time, more heterogeneity in tariff cuts widens the
relative differences in simulated impacts between the TE and standard aggregators. The
equivalent variation measure of consumer welfare increases in all scenarios and under all
aggregation methodologies (see consumer surplus in Fig. 4). This is a standard result for
tariff reduction in Armington models, and is due to decreasing consumer prices for beef.
Producer surplus, on the other hand, decreases due to the reductions in beef producer
price and domestic supply. Consumer and producer surplus changes point to the same
direction using all tariff aggregation approaches. However, we also note that there are
key differences in the magnitude of net welfare increases. In fact, TRIMAG systematically
delivers the highest impacts regarding all items of the welfare calculation. For the
homogenous cuts scenario, the net welfare impact of TRIMAG (90 million EUR) is almost
twice as high as the net welfare impact computed relying on the fixed weights approach (50
million EUR). Simulated net welfare gains are the lowest using the TE approach while
results using the fixed weight approach are between the other two aggregators. The order
of simulated impacts is consistent with the impacts on import prices, domestic prices and
production as presented above. Introducing more heterogeneity in the tariff schedule
enlarges the gap between simulated impacts across the aggregators. For example, in the
homogeneous cuts scenario the increases in simulated consumer surplus with the TE
aggregator are only marginally below the simulated changes using the fixed weight
aggregator. In contrast, the impact in the heterogeneous cuts scenario is more than three
times larger using the fixed weight aggregator than using the TE approach. When comparing
simulated welfare changes in the two scenarios, we note that making two tariff lines
exempt from the cuts obviously decreases welfare gains. Returning to the previous example,
simulated increase in consumer surplus for the TE aggregator in the heterogeneous cut
scenario is only about one third of the impact in the uniform cut scenario. The impacts on
consumer surplus, producer surplus and net welfare consequently mirror the different
impacts on the import prices between the tariff aggregators. Again, simulations with the
TRIMAG tariff cuts provide the largest impacts, followed by the fixed weight and TE
approaches. Finally, it should be noted that whether an ad valorem equivalent approach
(fixed weight and TE aggregators) or an explicit TRQ function approach (TRIMAG) is used
for modelling TRQs strongly affects the simulated tariff revenue impacts. Using the ad
valorem equivalent approach scenario, impacts on tariff revenues are negative because
increasing beef imports (quantity effect) do not compensate for the decrease in tariff
rates (price effect). With the explicit TRQ function approach of TRIMAG, the increase in
imports pushes the TRQ regime into an overfill position, and therefore beef imports above
the quota limit face reduced out-of-quota duties. That generates an increase in tariff
revenues in both scenarios. On the other hand, the decrease in the out-of-quota duties has
a significant impact on the quota rents. Quota rents decrease in both scenarios,
indicating that the overprotective part of the duty is fully eroded after tariff cuts and
consequently the unit quota rent decreases22. Two considerations concerning quota rents
and tariff revenues are relevant here. Firstly, the magnitude of the tariff revenue and
quota rent changes is significantly smaller than the changes in producer and consumer
surplus (for all aggregators and scenarios). Secondly, in TRIMAG, the increase in tariff
revenues and the decrease in quota rents almost neutralize each other (the combined effect
remains below 2 million euros in both scenarios). Although the impacts on tariff revenues
and quota rents may be significant for government revenues, they are not decisive for the
direction of net welfare changes. Net welfare change is mostly defined by the impacts on
import and domestic prices through their effect on consumer and producer surplus.

<h>CONCLUSIONS</h>
-----------

Market access policies, and import tariffs in particular, are defined at a finer product
detail than the one at which applied equilibrium models operate. This requires aggregating
data on trade and market access, which leads both to an aggregation bias in the simulated
results and to a departure from exact implementation of negotiated tariff schedules. This
paper develops a two-stage modelling approach, based on the TE and TRIMAG tariff
aggregators, to reduce aggregation bias in applied trade modelling. Three sources of
aggregation bias are focussed on: substitution effects at the tariff line, TRQ regime
shifts, and overprotective part of the duty. The tariff aggregators are tested against
tariff dismantling scenarios for the Swiss beef market, including a standard (fixed
weight) aggregator for comparison purposes. The three above-mentioned sources of
aggregation bias characterize many agri-food markets and particularly the Swiss beef
market since: a) the product heterogeneity of the beef tariff lines is sufficiently large
to induce large substitution effects; b) the market is regulated by a complex system of
TRQs; and c) the overprotective part of the duties varies to a great extent between the
beef tariff lines. The simulation results indicate that standard (fixed weight)
aggregators do not appropriately take into account either substitution effects at the
tariff line level, or TRQ regime shifts, or possible overprotection in duties, and so they
tend to provide biased estimates of the gains from trade liberalisation in terms of
simulated trade and welfare implications. Firstly, we find that the standard aggregator
overestimates the trade liberalisation impacts on traded quantities, specifically when
tariff cuts are heterogeneous. This is partly due to ignoring the substitution effect on
the import demand, which leads to larger tariff cuts on the bilateral trade links.
Ignoring TRQ regime shifts further contributes to the overestimated tariff cuts derived
using the standard method, confirming previous findings in the literature (Himics and
Britz, 2016). Secondly, simulated impacts with the standard aggregator on import prices,
producer prices, production and welfare are found to be in between the impacts derived
using the TE and TRIMAG approaches. This result shows a considerable bias in simulated
welfare gains using standard methods, and drives the attention to the importance of TRQ
modelling. On the one hand, net welfare impacts are reduced to one-third by using the TE
aggregator, which shifts TRQ modelling from the core PE model to the standalone tariff
aggregation module at the tariff line level. On the other hand, net welfare impacts are
even increased by using the TRIMAG approach, which keeps the explicit beef TRQ functions
(e.g. commodity level) of the core PE model. Thirdly, by comparing result of the
homogenous and heterogeneous tariff cut scenarios, it was demonstrated that the
aggregation bias increases with greater dispersion in tariffs or tariff cuts. Real-life
tariff schedules typically show large tariff dispersion, which is often increased by trade
negotiations conducted at the tariff line level. This finding supports the relevance of
the proposed aggregators for direct policy support. Fourthly, the different simulated
impacts between the TE and TRIMAG aggregator suggest that information on the
overprotective part of the duties further reduces aggregation bias. Consequently, using
data at detailed product level to estimate the height of the unit quota rent under a TRQ
regime is well warranted, and further motivates statistical data collection and data
processing directly on observable unit quota rents and on domestic prices. A final
consideration concerns the technical implementation of the TE and TRIMAG aggregators as
standalone modules linked to a large-scale PE model (CAPRI). Linking the aggregation
modules to CAPRI does not require significant changes in the original model. In fact, the
trade policy representation simplifies in CAPRI for the TE approach by shifting TRQ
modelling into the standalone tariff aggregation module. Given that the proposed tariff
aggregation approaches only simulate demand side adjustments, the respective aggregation
modules are relatively easy to set up and solve numerically, and detailed trade statistics
and policy data are available to parameterize them. Against this background we can state
that the proposed tariff aggregation techniques can be implemented in existing modelling
systems without the heavy burden of modifying core model structures and without
jeopardizing the numerical feasibility of the overall modelling system. Consequently, more
widespread use of advanced tariff aggregation techniques for applied trade modelling seems
to be within reach. The above results support the findings of Countryman and Narayanan
(2017), which highlight that the simplified ad valorem representation of trade policy
measures, such as specific tariffs in their case or TRQs in this paper, lead to biased
simulated price effects on the domestic markets. The biased welfare results, identified
above, have been also highlighted in the literature. Gouel et al. (2011), for example,
simulate smaller welfare gains after extending their CGE modelling framework to the
product level and considering tariff line level exceptions (sensitive products). Our
strategy to better exploit tariff line level data by using standalone tariff aggregation
modules is in line with Britz and van der Mensbrugghe (2016) who advocates avoiding
aggregation in model databases the utmost to reduce the induced bias in ex ante policy
evaluation. However, several caveats to the proposed approaches must be emphasised. Both
the TRIMAG and the TE aggregators only account for the consumption gains from trade and
not for any production or specialization gains. Whether this is an acceptable restriction
remains case specific. In the empirical application presented in this paper, the potential
consumption gains from liberalising the beef trade largely outweigh the losses linked to
domestic production, and therefore the assumption is viable. Although the test scenarios
intentionally focus on a specific market and country, the approach also has the potential
to correct significant bias stemming from heterogeneous tariff cuts in more complex and
broader (global) applied trade liberalisation scenarios. With the proposed tariff
aggregators, negotiated tariff schedules can be introduced to applied equilibrium models
directly, without first aggregating tariff cuts over tariff lines. Our simulation results
suggest that they also reduce aggregation bias, consequently enhancing the potential
contributions of trade modelling to evidence based policy making.

<h>DISCLAIMER</h>
----------

The views expressed in this article are purely those of the authors and may not in any
circumstances be regarded as stating an official position of the European Commission or
the Federal Office for Agriculture (FOAG). The work was carried out while Giulia Listorti
was Scientific Advisor at the Swiss Federal Office for Agriculture.


<h>REFERENCES</h>
----------

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<ART>Sparse Bayesian time-varying covariance estimation in many dimensions
=====================================================================

Authors: Gregor Kastner
DOI: 10.1016/j.jeconom.2018.11.007
Year: 2019  |  Pages: 98-115
ASJC codes: 2002
Keywords: Curse of dimensionality, Dynamic correlation, Factor stochastic volatility, Minimum variance portfolio, Shrinkage

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We address the curse of dimensionality in dynamic covariance estimation by modeling the underlying co-volatility dynamics of a time series vector through latent time-varying stochastic factors. The use of a global–local shrinkage prior for the elements of the factor loadings matrix pulls loadings on superfluous factors towards zero. To demonstrate the merits of the proposed framework, the model is applied to simulated data as well as to daily log-returns of 300 S&P 500 members. Our approach yields precise correlation estimates, strong implied minimum variance portfolio performance and superior forecasting accuracy in terms of log predictive scores when compared to typical benchmarks.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The joint analysis of hundreds or even thousands of time series exhibiting a potentially
time-varying variance–covariance structure has been on numerous research agendas for well
over a decade. In the present paper we aim to strike the indispensable balance between the
necessary flexibility and parameter parsimony by using a factor stochastic volatility (SV)
model in combination with a global–localshrinkage prior. Our contribution is threefold.
First, the proposed approach offers a hybrid cure to the curse of dimensionality by
combining parsimony (through imposing a factor structure) with sparsity (through employing
computationally efficient absolutely continuous shrinkage priors on the factor loadings).
Second, the efficient construction of posterior simulators allows for conducting Bayesian
inference and prediction in very high dimensions via carefully crafted Markov chain Monte
Carlo (MCMC) methods made available to end-users through the R (R Core Team, 2017) package
factorstochvol (Kastner, 2017). Third, we show that the proposed method is capable of
accurately predicting covariance and precision matrices which we assess via statistical
and economic forecast evaluation in several simulation studies and an extensive real-world
example. Concerning factor SV modeling, early key references include Harvey et al. (1994),
Pitt and Shephard (1999) and Aguilar and West (2000) which were later picked up and
extended by e.g. Philipov and Glickman (2006), Chib et al. (2006), Han (2006), Lopes and
Carvalho (2007), Nakajima and West (2013), Zhou et al. (2014) and Ishihara and Omori
(2017). While reducing the dimensionality of the problem at hand, models with many factors
are still rather rich in parameters. Thus, we further shrink unimportant elements of the
factor loadings matrix to zero in an automatic way within a Bayesian framework. This
approach is inspired by high-dimensional regression problems where the number of
parameters frequently exceeds the size of the data. In particular, we adopt the approach
brought forward by Caron and Doucet (2008) and Griffin and Brown (2010) who suggest to use
a special continuous prior structure – the Normal-Gamma prior – on the regression
parameters (in our case the factor loadings matrix). This shrinkage prior is a
generalization of the Bayesian Lasso (Park and Casella, 2008) and has recently received
attention in the econometrics literature (Bitto and Frühwirth-Schnatter, 2018; Huber and
Feldkircher, 2017). Another major issue for such high-dimensional problems is the
computational burden that goes along with statistical inference, in particular when joint
modeling is attempted instead of multi-step approaches or rolling-window-like estimates.
Suggested solutions include Engle and Kelly (2012) who propose an estimator assuming that
pairwise correlations are equal at every point in time, Pakel et al. (2017) who consider
composite likelihood estimation, Gruber and West (2016) who use a decoupling–recoupling
strategy to parallelize estimation (executed on graphical processors), Lopes et al. (2018)
who treat the Cholesky-decomposed covariance matrix within the framework of Bayesian time-
varying parameter models, and Oh and Patton (2017) who choose a copula-based approach to
link separately estimated univariate models. We propose to use a Gibbs-type sampler which
allows to jointly take into account both parameter as well as sampling uncertainty in a
finite-sample setup through fully Bayesian inference, thereby enabling inherent
uncertainty quantification. Additionally, this approach allows for fully probabilistic in-
and out-of-sample density predictions. For related work on sparse Bayesian prior
distributions in high dimensions, see e.g. Kaufmann and Schumacher (2018) who use a point
mass prior specification for factor loadings in dynamic factor models or Ahelegbey et al.
(2016) who use a graphical representation of vector autoregressive models to select sparse
graphs. From a mathematical point of view, Pati et al. (2014) investigate posterior
contraction rates for a related class of continuous shrinkage priors for static factor
models and show excellent performance in terms of posterior rates of convergence with
respect to the minimax rate. All of these works, however, assume homoskedasticity and are
thus potentially misspecified when applied to financial or economic data. For related
methods that take into account heteroskedasticity, see e.g. Nakajima and West (2013, 2017)
who employ a latent thresholding process to enforce time-varying sparsity. Moreover, Zhao
et al. (2016) approach this issue via dependence networks, Loddo et al. (2011) use
stochastic search for model selection, and Baştürk et al. (2018) use time-varying
combinations of dynamic models and equity momentum strategies. These methods are typically
very flexible in terms of the dynamics they can capture but are applied to moderate
dimensional data only. We illustrate the merits of our approach through extensive
simulation studies and an in-depth financial application using 300 S&P 500 members. In
simulations, we find considerable evidence that the Normal-Gamma shrinkage prior leads to
substantially sparser factor loadings matrices which in turn translate into more precise
correlation estimates when compared to the usual Gaussian prior on the loadings.1 In the
real-world application, we evaluate our model against a wide range of alternative
specifications via log predictive scores and minimum variance portfolio returns. Factor SV
models with sufficiently many factors turn out to imply extremely competitive portfolios
in relation to well-established methods which typically have been specifically tailored
for such applications. Concerning density forecasts, we find that our approach outperforms
all included competitors by a large margin. The remainder of this paper is structured as
follows. In Section 2, the factor SV model is specified and the choice of prior
distributions is discussed. Section 3 treats statistical inference via MCMC methods and
sheds light on computational aspects concerning out-of-sample density predictions for this
model class. Extensive simulation studies are presented in Section 4, where the effect of
the Normal-Gamma prior on correlation estimates is investigated in detail. In Section 5,
the model is applied to 300 S&P 500 members. Section 6 wraps up and points out possible
directions for future research.

<hs>  Factor SV model</hs>
  ~~~~~~~~~~~~~~~

Third, note that even though the joint distribution of the data is conditionally Gaussian,
its stationary distribution has thicker tails. Nevertheless, generalizations of the
univariate SV model to cater for even more leptokurtic distributions (e.g. Liesenfeld and
Jung, 2000) or asymmetry (e.g. Yu, 2005) can straightforwardly be incorporated in the
current framework. All of these extensions, however, tend to increase both sampling
inefficiency as well as running time considerably and could thus preclude inference in
very high dimensions.

<h>STATISTICAL INFERENCE</h>
---------------------

There are a number of methods to estimate factor SV models such as quasi-maximum
likelihood (e.g. Harvey et al., 1994), simulated maximum likelihood (e.g. Liesenfeld and
Richard, 2006; Jungbacker and Koopman, 2006), and Bayesian MCMC simulation (e.g. Pitt and
Shephard, 1999; Aguilar and West, 2000; Chib et al., 2006; Han, 2006). For high
dimensional problems of this kind, Bayesian MCMC estimation proves to be a very efficient
estimation method because it allows simulating from the high dimensional joint posterior
by drawing from lower dimensional conditional posteriors.

<hs>  MCMC estimation</hs>
  ~~~~~~~~~~~~~~~

The above sampling steps are implemented in an efficient way within the R package
factorstochvol. Table 1 displays the empirical run time in milliseconds per MCMC
iteration. Note that using more efficient linear algebra routines such as Intel MKL leads
to substantial speed gains only for models with many factors. To a certain extent,
computation can further be sped up by computing the individual steps of the posterior
sampler in parallel. In practice, however, doing so is only useful in shared memory
environments (e.g. through multithreading/multiprocessing) as the increased communication
overhead in distributed memory environments easily outweighs the speed gains.

<hs>  The shrinkage prior effect: An illustration</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Fig. 1 shows smoothed kernel density estimates of posterior loadings under the different
prior assumptions. The signs of the loadings have not been identified so that a multimodal
posterior distribution hints at a “significant” loading whereas a unimodal posterior hints
at a zero loading, see also Frühwirth-Schnatter and Wagner (2010). It stands out that only
very little shrinkage is induced by the standard Gaussian prior. The other priors,
however, impose considerably tighter posteriors. For the nonzero loadings on factor one,
e.g., the row-wise Bayesian Lasso exhibits the strongest degree of shrinkage. Little
difference between the various shrinkage priors can be spotted for the nonzero loadings on
factor two. Turning towards the zero loadings, the strongest shrinkage is introduced by
both variants of the Normal-Gamma prior, followed by the different variants of the
Bayesian Lasso and the standard Gaussian prior. This is particularly striking for the
loadings on the superfluous third factor. The difference between row- and column-wise
shrinkage for the Lasso variants can most clearly be seen in row 9 and column 3,
respectively. The row-wise Lasso captures the “zero-row” 9 better, while the column-wise
Lasso captures the “zero-column” 3 better. Because of the increased element-wise shrinkage
of the Normal-Gamma prior, the difference between the row-wise and the column-wise variant
are minimal. In the context of covariance modeling, however, factor loadings can be viewed
upon as a mere means to parsimony, not the actual quantity of interest. Thus, Fig. 2
displays selected time-varying correlations. The top panel shows a posterior interval
estimate (mean plus/minus two standard deviations) for the correlation of series 1 and
series 2 (which is nonzero) under all five prior settings; the bottom panel depicts the
interval estimate for the correlation of series 9 and 10 (which is zero). While the
relative differences between the settings in the nonzero correlation case are relatively
small, the zero correlation case is picked up substantially better when shrinkage priors
are used. Posterior means are closer to zero and the posterior credible intervals are
tighter.

<hs>  Medium dimensional Monte Carlo study</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

An overall comparison of the errors under different priors is provided in Table 4 which
lists RMSEs and MAEs for all prior settings, averaged over the non-trivial correlation
matrix entries as well as time. Note again that results under the Lasso prior are
sensitive to the particular choices of the global shrinkage hyperparameters as well as the
choice of row- or column-wise shrinkage, which is hardly the case for the Norma-Gamma
prior. Interestingly, the performance gains achieved through shrinkage prior usage are
higher when absolute errors are considered. This is coherent with the extremely high
kurtosis of Normal-Gamma-type priors which, while placing most mass around zero, allow for
large values.

<h>APPLICATION TO S&P 500 DATA</h>
---------------------------

The presentation consists of two parts. First, we exemplify inference using a multivariate
stochastic volatility model and discuss the outcome. Second, we perform out-of-sample
predictive evaluation and compare different models. To facilitate interpretation of the
results discussed in this section, we consider the GICS5  classification into 10 sectors
listed in Table 6.

<hs>  A four-factor model for 300 S&P 500 members</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

To keep graphical representation feasible, we only focus on the latest 2000 returns of our
data set, i.e. 5/3/2006 to 12/31/2013. This time frame is chosen to include both the 2008
financial crisis as well as the period before and thereafter. Furthermore, we restrict our
discussion to a four-factor model. This choice is somewhat arbitrary but allows for a
direct comparison to a popular model based on four observed (Fama–French plus Momentum)
factors. A comparison of predictive performance for varying number of factors is discussed
in Section 5.2; the Fama–French plus Momentum model is introduced in Section 5.3. Median
posterior factor loadings are visualized in Fig. 5. In the top panel it can be seen that
all series significantly load on the first factor which consequently could be interpreted
to represent the joint dynamics of the wider US equity market. Investigating the second
factor, it stands out that due to the use of the Normal-Gamma prior a considerable amount
of loadings are shrunk towards zero. Main drivers are all in the sector Utilities. Also,
companies in sectors Consumer Staples, Health Care and (to a certain extent) Financials
load positively here. Both the loadings on factor 3 as well as the loadings on factor 4
are substantially shrunk towards zero. Exceptions are Energy and Materials companies for
factor 3 and Financials for factor 4. The corresponding factor log variances are displayed
in Fig. 6. Apart from featuring similar low- to medium frequency properties, each process
exhibits specific characteristics. First, notice the sharp increase of volatility in early
2010 which is mainly visible for the “overall” factor 1. The second factor (Utilities)
displays a pre-crisis volatility peak during early 2008. The third factor, driven by
Energy and Materials, shows relatively smooth volatility behavior while the fourth factor,
governed by the Financials, exhibits a comparably turbulent volatility evolution.

<hs>  Predictive likelihoods for model selection</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Even for univariate volatility models evaluating in- or out-of-sample fit is not
straightforward because the quantity of interest (the conditional standard deviation) is
not directly observable. While in lower dimensions this issue can be circumvented to a
certain extent using intraday data and computing realized measures of volatility, the
difficulty becomes more striking when the dimension increases. Thus, we focus on
iteratively predicting the observation density out-of-sample which is then evaluated at
the actually observed values. Because this approach involves re-estimating the model for
each point in time, it is computationally costly but can be parallelized in a trivial
fashion on multi-core computers.

<h>CONCLUSION AND OUTLOOK</h>
----------------------

Further research could be directed towards incorporating prior knowledge into building the
hierarchical structure of the Normal-Gamma prior, e.g. by choosing the global shrinkage
parameters according to industry sectors. Alternatively, Villani et al. (2009) propose a
mixture of experts model to cater for smoothly changing regression densities. It might be
fruitful to adopt this idea in the context of covariance matrix estimation by including
either observed (Fama–French) or latent factors as predictors and allowing for other
mixture types than the ones discussed there. While not being the focus of this work, it is
easy to extend the proposed method by exploiting the modular nature of Markov chain Monte
Carlo methods. In particular, it is straightforward to combine it with mean models such as
(sparse) vector autoregressions (e.g., Bańbura et al., 2010; Kastner and Huber, 2018),
dynamic regressions (e.g., Korobilis, 2013), or time-varying parameter models (e.g., Koop
and Korobilis, 2013; Huber et al., 2019).


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<ART>Sustainable agreements on stochastic river flow
===============================================

Authors: Erik Ansink, Harold Houba
DOI: 10.1016/j.reseneeco.2016.02.005
Year: 2016  |  Pages: 92-117
ASJC codes: 2002
Keywords: Folk Theorem, Renegotiation-proofness, Repeated sequential game, River sharing, Sustainable agreements, Water allocation

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Many river sharing agreements in transboundary river basins are inherently unstable. Due to stochastic river flow, agreements may be broken in case of drought. The objective of this paper is to analyze whether river sharing agreements can be self-enforcing, or sustainable. We do so using an infinitely-repeated sequential game that we apply to several classes of agreements. To derive our main results we apply the equilibrium concepts of subgame-perfect equilibrium and renegotiation-proof equilibrium to the river sharing problem. We show that, given the upstream-downstream asymmetry, sustainable agreements allow downstream agents to reap the larger share of the benefits of cooperation.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

We extend and apply the theory of repeated games to the river sharing problem. Our main
contribution is the design of agreements that are sustainable to stochastic river flow in
a dynamic setting. Doing so, we add to the rapidly growing literature on the analysis of
solutions to the river sharing problem (cf. Béal et al., 2013; van den Brink et al., 2012;
Ambec et al., 2013), which has largely ignored dynamics and stochasticity. In an
international river basin, when water is scarce, countries may exchange water for side
payments (Dinar, 2006; Carraro et al., 2007). This type of exchange is generally
formalized in a river sharing agreement. The aim of river sharing agreements is to
increase the overall efficiency of water use. This increase in efficiency can be
obstructed by the stochastic nature of river flow, because countries may find it
profitable to break the agreement in case of drought (Dinar et al., 2015; Ward, 2013). A
recent example is Mexico's failure to meet its required average water deliveries under the
1944 US-Mexico Water Treaty in the years 1992–1997 (Gastélum et al., 2009). Additional
case study evidence on agreement breakdowns because of droughts can be found, for
instance, in Barrett (1994) and Beach et al. (2000). Only a minority of current
international agreements take into account the variability of river flow (de Stefano et
al., 2012). Most agreements do not; they either allocate fixed or proportional shares, or
they are ambiguous in their schedule for water allocation. Both the efficiency and
stability (Bennett and Howe, 1998; Bennett et al., 2000; Ansink and Ruijs, 2008; Ambec et
al., 2013) of such agreements may be hampered. These effects could be worsened by the
impacts of climate change on river flow. In order to accommodate for stochastic river
flow, Kilgour and Dinar (2001) developed a flexible river sharing agreement that provides
an efficient allocation for every possible level of river flow. This agreement maximizes
the overall benefits of water use, after which side payments are made such that each
country benefits from cooperation. This flexible agreement assures efficiency, but not
stability because it ignores the repeated interaction of countries over time. Countries
have an incentive to defect from the agreement when the benefits of defecting outweigh the
benefits of compliance. Note that there is no supra-national authority that can enforce
this type of international agreements. This implies that a stable agreement has to be
self-enforcing or sustainable, in the sense that each agent should have an incentive to
comply with the agreement. In such a setting, application of repeated-game theory to the
setting of river sharing seems natural, but to the best of our knowledge, this has not
been done yet.1 Given the asymmetry imposed by the geography of the river, we adopt an
infinitely-repeated sequential game, in which upstream agents move before downstream
agents.2 The Folk Theorem for infinitely-repeated sequential games is a limit result on
the discount factor. For practical purposes, the issue is firstly, given some discount
factor, how to construct sustainable agreements, and secondly whether certain classes of
agreements have properties that may be appealing for implementation by policy makers. For
instance, we will assess the effects of restrictions on per-period payoffs and we will
look at some disadvantages of fixed-payment agreements, which are common in practice. To
derive our main results we apply the Folk Theorem to the river sharing problem using the
equilibrium concepts of subgame-perfect equilibrium and renegotiation-proof equilibrium.
We will see that, given the upstream–downstream asymmetry, sustainable agreements allow
downstream agents to reap the larger share of the benefits of cooperation. This
distribution of gains is the opposite of some papers that assess agreements on river
sharing in a static setting (e.g. Ambec et al., 2013). Our results provide economic
intuition for an empirical result (downstream states managing to negotiate a substantial
share of upstream river water) that has, up till now, mostly been explained by political
factors (Dinar, 2009; Katz and Moore, 2011). In the next section we introduce our model.
We derive equilibrium conditions in Section 3, which we use in an example in Section 4.
After an intermezzo in Section 5 on the trade-off between efficiency and stability, we
continue in Sections 6 and 7 with a detailed analysis of actual agreements. Finally, in
Section 8, we provide some concluding remarks. Two appendices contain proofs as well as
detailed information on context and generalization of our analysis.

<hs>  Preliminaries</hs>
  ~~~~~~~~~~~~~

There are several focal allocations of river flow that will be used extensively in the
remainder of the paper: the Nash allocation,4 the efficient allocation and the minmax
allocation. Definitions of the Nash allocation and efficient allocation are given below,
while the minmax allocation is the subject of Proposition 1. Nash allocation Because of
increasing benefits of water use, the Nash allocation is evident in the absence of water
trade or other types of agreements on water use. Efficient allocation With a strictly
concave quasi-linear utility function as in (1), the efficient allocation is unique and
equal to utilitarian welfare maximization as in e.g. Kilgour and Dinar (2001) and Houba et
al. (2014). The interesting and non-trivial case occurs when water is scarce: Water
scarcity Realizations without incentives to cooperate can be ignored because any efficient
agreement will specify no cooperation for each of these realizations, which is trivially
sustainable. Our model setup is consistent with much of the river sharing literature. The
case of two agents (Ansink and Ruijs, 2008; Houba, 2008) provides no limitation for
reasons similar to infinitely-repeated games with n players and full dimensionality. Full
dimensionality is assured in river sharing problems because with n players the monetary
transfers allow redistribution of transferable utility in all n utility dimensions. By
focusing on two agents instead of the general case with more agents and more realistic
river geographies (Ansink and Houba, 2012; van den Brink et al., 2012), we are able to
avoid some complexity and excessive notation. It also provides a better understanding of
the issues involved in repeated interaction of the agents over time in the presence of
stochastic river flow. In Appendix A, we elaborate on the general case.

<hs>  River sharing agreements</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~

We proceed to describe the possibility of river sharing agreements between the two agents.
Our focus is on what we call ‘implicit’ agreements. Such an agreement coincides with a set
of agents’ strategies in the infinitely-repeated sequential game that can be sustained in
equilibrium, and which improves upon the Nash allocation. It does not require outside
enforcement. An agreement (and thereby the agents’ strategies) specifies the following
three elements: An allocation rule for river flow; A payment rule for monetary transfers;
and Punishment strategies in case one of the agents deviates from the agreement (which may
also involve monetary transfers). In the infinitely-repeated sequential game, that we
introduce below, both the allocation of water and the payment may be contingent on
realized river flow as in Kilgour and Dinar (2001). In reality, however, we also observe
lump-sum payments and simpler allocation rules, including fixed and proportional
allocations (Ansink and Ruijs, 2008; Drieschova et al., 2008). Punishment strategies are
essential for the sustainability of the agreement because, in absence of a supra-national
authority, agreements are non-binding. Punishment strategies determine what happens upon
deviation and range from simple trigger strategies to more advanced strategies that assure
ex post credibility of the punishment. In actual agreements on river flow allocations,
punishment strategies are often lacking, although many do contain clauses on conflict
resolution (Beach et al., 2000; Ward, 2013).

<hs>  Minmax values</hs>
  ~~~~~~~~~~~~~

The Folk Theorem for infinitely-repeated sequential games states that any utility vector
that yields each agent more than his minmax value can be supported as an SPE (subgame-
perfect equilibrium) utility vector for sufficiently large discount factors (Wen, 2002).
Following this reference, we start our analysis by deriving the minmax values in the river
sharing problem. We do this in Appendix A, where we also discuss the general case (i.e.
more than two agents) as well as the implications of assuming increasing benefit functions
for the minmax values. We state the following result. For every realization (e1, e2),
agent i's minmax value is bi(ei). The agents’ minmax values coincide with the unique Nash
equilibrium utilities and can be supported as a stationary SPE outcome path for all
discount factors δ ∈ [0, 1) by the stationary strategies ‘always play the Nash
equilibrium’. Because no SPE strategy is worse than the minmax value, this stationary SPE
not only supports the worst possible outcome, but it also punishes at least as harsh as
more sophisticated stick-and-carrot strategies as in e.g. Abreu (1988). This result has an
important implication in that the Folk Theorem can be derived within the class of trigger
strategies, which simplifies the analysis (details are in Appendices A and B). Trigger
strategies Both agents use trigger strategies in which deviation from cooperative play
under the agreement is punished by non-cooperative play forever (i.e. the Nash
allocation).

<h>EQUILIBRIUM ANALYSIS</h>
--------------------

Any agreement that satisfies both (4) and (5) for each realization (e1, e2) is able to
sustain cooperation. This requires a choice of allocation and payment rules that is
sufficiently flexible such that the bounds are not violated for any possible realization
of river flow. Note the asymmetry in these bounds with respect to the payments; the lower
bound always depends upon the realization (e1, e2) whereas the upper bound is independent
of this realization and stated in terms of expectation. This asymmetry is caused by the
extensive form of the game, which requires agent 2 to provide a minimum compensation to
agent 1 for passed water in the current period, which enters the current realization in
the lower bound. In addition, both bounds contain terms that reflect the expected benefits
of cooperation in future periods. In the next section we use these bounds to illustrate
the choice of a payment rule given the unique allocation rule that maximizes utilitarian
welfare.

<h>EXAMPLE</h>
-------

In this section we show how bounds (4) and (5) can be used to construct a payment rule for
monetary transfers given a fixed parameter value for the discount factor, using a simple
illustrative example that will recur throughout the paper. In order to do so, we make two
additional assumptions. Two realizations of river flow Efficient agreement Fig. 1 shows
the polygon for selected parameter values, illustrating the range of possible combinations
of payments that provide sustained cooperation under Assumptions 2–4. Any point in the
graph represents a payment rule, but only those in the shaded area sustain cooperation.
Somewhat counter-intuitively, Fig. 1 illustrates the possibility of a negative payment
under one of the two possible realizations of river flow. This gives the striking
possibility that agent 1 delivers water and a payment to agent 2. Obviously, a negative
payment under one realization is accompanied by a relatively large positive payment under
the alternative realization of river flow. This possibility of negative payments makes
clear that, while theoretically sound, some sustainable payment rules may be inapplicable
in real life situations. Fig. 2 shows a comparison of results for various values of the
discount parameter δ. The figure illustrates that there is no feasible payment rule for
low levels of the discount factor (for the parameter values in the figure, the threshold
is δ = (5/7) ≈ 0.7). At the threshold, the bounds for the realization of low river flow
first converge and below this threshold, they switch place and diverge such that there are
no combinations of payments that provide sustained cooperation. The intuition for this
result is standard in that a lower δ reduces the expected present value of the benefits of
cooperation in all future periods, which are compared with the benefits of non-cooperation
in the current period. Summarizing, given a fixed parameter value for the discount factor
and given trigger strategies, the illustration in Fig. 1 shows how to construct
sustainable agreements. Such agreements are not possible for a sufficiently low discount
factor and some sustainable payment rules may be unrealistic if they include negative
payments. Because it is not clear how such agreements could ever be put into practice, we
assess several subsets of agreements that do not allow negative payments in Sections 6 and
7, in which we will also drop Assumptions 3 and 4.

<h>THE SUSTAINABILITY OF ACTUAL AGREEMENTS</h>
---------------------------------------

In this section we consider two subsets of agreements and assess their sustainability:
fixed-payment agreements and individually-rational agreements. The reasoning for assessing
these particular subsets is as follows. First, most existing agreements with payments
explicitly coupled to water deliveries employ fixed payments. Second – and related –
fixed-payment agreements reflect the lack of flexibility with respect to variability in
river flow (de Stefano et al., 2012; Giordano et al., 2014). Third, individually-rational
agreements offer more flexibility and they exclude the unrealistic and objectionable
option of payoffs lower than minmax payoffs (including negative payments as discussed in
Section 4). Both subsets serve as a realistic benchmark for the design of more sustainable
agreements in Section 7. Note that we will not need Assumptions 3 and 4.

<hs>  Fixed-payment agreements</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~

By Assumption 1 on water scarcity, the left-hand side is positive for xc(e1, e2) = x*(e1,
e2) and these belong to a well-defined compact set of agreements xc(e1, e2) that admit a
non-negative left-hand side. For the subset of agreements xc(e1, e2) that admit a positive
left-hand side, as δ goes to 1, the left-hand side converges to some positive number while
the right-hand side converges to 0, so that the inequality holds. Therefore, we know that
for this particular subset of agreements xc(e1, e2) there exists a threshold discount
factor above which the range of sustainable payment rules is non-empty. Obviously,
agreements xc(e1, e2) for which the left-hand side is either zero or negative cannot be
sustained for any δ ∈ [0, 1). One may interpret fixed-payment agreements as insurance
contracts where downstream pays a fixed amount for a flexible scheme of water deliveries.
In this interpretation, there is nothing against such agreements. One problem of fixed-
payment rules, however, is that they may cause payoffs lower than minmax payoffs for some
realizations of river flow. This property makes such rules unattractive for application in
practice. We will see in Section 6.2 that, for the example of Section 4, any fixed-payment
agreement violates this condition.

<hs>  Individually-rational agreements</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Whether these restrictions hold in practice is an open question. The concept of individual
rationality directly suggests that countries would never sign an agreement that yields
them payoffs lower than their minmax payoffs. Yet, this situation could occur for fixed
payment agreements as is illustrated by Fig. 4. Even proportional allocation rules, often
advocated as offering flexibility to adapt to variability of river flow (cf. McCaffrey,
2003; Drieschova et al., 2008) fall within this class if they rely on fixed payments and
may therefore not be individually rational (Ansink and Ruijs, 2008). When payments are
flexible rather than fixed – and individually rational agreements allow for this – this
barrier is resolved. The combination of a flexible allocation rule and flexible payments
was suggested by Kilgour and Dinar (2001) to achieve an “efficient schedule” of river
water allocation. Kilgour and Dinar (2001) consider efficient and individually rational
agreements and therefore our Proposition 3 can be compared to their result. Specifically,
this proposition indicates that their efficiency result may hold, but these “efficient
schedules” are not stable for sufficiently low δ. This difference illustrates the
importance of considering repeated interaction between agents in a river basin. In
addition, the consideration of repeated interaction may cause two additional effects. One
is that it may affect the distribution of the benefits of cooperation (see below). The
other consequence is that stability may come at the cost of reduced efficiency (see
Section 5). Both effects are absent in the (static) model by Kilgour and Dinar (2001).
Note that the subset of individually-rational agreements contains various types of
agreements. One example is a price-dependent agreement, in which the allocation rule is
the efficient allocation and the payment implements the efficient water price, such that
marginal benefits of water use are equal to both agents. This type of agreement mimics an
international water market (cf. Ansink and Houba, 2012). An alternative example is the
(asymmetric) Nash-bargaining solution, which we analyze in Section 7.1. Recall the
interpretation of fixed-payment agreements as insurance contracts. Individually-rational
agreements can also be interpreted as insurance contracts with a stochastic price sc(e1,
e2) that depends upon the realization of river flow. This means that next to the risk over
the allocation of water there is also risk with respect to this price. Because monetary
payments enter the agents’ quasi-linear utility functions in (1) as the linear term,
agents are risk neutral with respect to this category of risk. Consequently, they are
indifferent between individually-rational agreements and fixed-payment contracts with the
same allocation and payment E{sc(e1, e2)}.

<h>NEGOTIATING A SUSTAINABLE AGREEMENT</h>
-----------------------------------

In this section, we focus on agreements that are the outcome of a negotiation procedure
and assess under which conditions such agreements can be sustained in equilibrium.
Compared with the agreements assessed in Section 6, the current agreements potentially
offer more flexibility. Here, our aim is not to assess an exogenously given subset of
agreements, but rather to endogenize the agreement given exogenous model parameters (e.g.
the discount factor δ and a weight α, introduced below). Nevertheless, to guide our
assessment we do need some structure on the types of agreements to assess and, through our
selection of equilibrium concepts, we focus on efficient agreements only. We will approach
such agreements using the equilibrium concepts of subgame-perfect equilibrium and
renegotiation-proof equilibrium. Nash-bargaining agreements are assessed to illustrate how
negotiations may lead to efficient and stable agreements. Renegotiation-proof agreements
show how this additional stability requirement affects the agreement design. As before, we
will not need Assumptions 3 and 4.

<hs>  Nash-bargaining agreements</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~

Note that application of the ANBS implies that we assume, to some extent, an ‘ideal’
setting where bargaining strengths are readily available and there are no restrictions
imposed by sustainability considerations or other factors at play (see Fig. 5 and its
discussion below). In general, the bargaining strength parameter can be based on factors
related to economic, political, or military dominance in the river basin. For specific
case studies, an empirical estimate of bargaining strength can be obtained by evaluation
of an existing agreement. Assuming that such an agreement is a Nash bargaining solution
obtained in a setting not too different from the ‘ideal’ setting, its outcome can be used
to derive the corresponding α parameter. Houba et al. (2014) provide a framework for
making such a derivation. For Nash-bargaining agreements, given weight α, we show in our
next result that any efficient agreement that improves upon the utilities under the minmax
allocation xN(e1, e2) = (e1, e2) is an SPE for sufficiently large δ < 1. The difference
with Proposition 3 is subtle. By construction, the ANBS as applied in (13) satisfies
Conditions (10) and (11) that describe the set of individually-rational agreements and,
therefore, Nash-bargaining agreements are a subset of this set. The Pareto efficiency of
Nash-bargaining agreements implies that the threshold discount factor for which an
agreement can be sustained will coincide with the one for the associated Pareto efficient
individually-rational agreement. As is standard in the literature on repeated games, we
present our result in terms of a threshold discount factor, above which subsets of
agreements can be sustained in equilibrium. For the practical purpose of this paper,
however, the real issue is how to construct sustainable agreements when δ is given. In our
case this means how to construct the range of sustainable Nash bargaining agreements. This
is why our next result consists of two parts: one in terms of a threshold lower bound on δ
and one in terms of a threshold upper bound on α. Before discussing these results, we
stress that Proposition 4 depends on the specific payment rule adopted in (13) which
limits its scope, see Footnote 12. The result by Ambec et al. (2013) is particularly
noteworthy, since they find that the downstream incremental distribution is actually the
least sustainable agreement (Ambec et al., 2013, Proposition 3). This result is the
converse of our result. The reason for this opposite result is the setting of the
analysis; Ambec et al. (2013) present a static analysis and thereby ignore the importance
of repeated interaction. This repetition turns out to completely reverse the relative
advantage of upstream–downstream location in the river basin. In a static setting, the
upstream agent can act like the hegemon to exploit his geographic advantage. In a dynamic
setting, however, agents depend on each other and the downstream agent has an advantage in
timing as explained in Footnote 2. The downstream incremental distribution has been
criticized for being an extreme solution. In the next subsection, however, we will see
that the requirement of renegotiation-proofness adds even more credibility to this
‘extreme’ solution.

<hs>  Renegotiation-proof equilibria</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In this section we assess the implications of requiring agreements to satisfy
renegotiation-proofness. Up till here, we assumed trigger strategies, but these strategies
have an important disadvantage: the agent who carries out the punishment by switching to
non-cooperative play is also punishing himself. This gives the punisher an incentive to
abolish his punishment, and re-negotiate with the defector in order to revert to
cooperative play, which Pareto-dominates the non-cooperative path. As a result,
punishments by trigger strategies lack credibility. In response to this lack of
credibility, the key idea of renegotiation-proof equilibria (RPE) is to construct strategy
profiles with punishments that include a non-negative reward to the punisher. Based on the
concept of weakly renegotiation-proof equilibrium proposed by Farrell and Maskin (1989),
our following result provides additional support for solutions in which the downstream
agent gains most. Appendix B contains additional background information on RPE as well as
an extensive proof of Proposition 5. We will first summarize the results of Appendix B
before stating our main results. Since we are interested in Pareto efficient solutions, we
focus, without loss of generality, on sustaining Nash bargaining agreements in RPE. In
order to sustain the Nash bargaining agreement α0 ∈ [0, 1), we introduce two punishment
paths, one for each agent. The punishment path for agent 1 corresponds to the Nash
bargaining agreement α1 = 0 in every period, a path on which agent 1 has no incentive to
deviate. The punishment path for agent 2 is somewhat more involved. In the first period of
this path, agent 1 does not deliver any water and agent 2 pays a penalty that is equal to
the present value of the entire expected net surplus of all future periods from the second
period onwards, which is independent of the current realization. From the second period
onward, we switch to the Nash bargaining agreement α2 = 0 in every period, which equals
agent 1's punishment path (we postpone an explanation). For the moment, agent 2's
punishment path coincides with agent 1's best RPE path. Therefore, agent 2's punishment
path is Pareto efficient from the second period onwards with unavoidable efficiency losses
only in the first period. In our next results, we state the theoretically largest set of
Pareto efficient RPE Nash bargaining agreements that are derived in Appendix B, using the
thresholds in (14) and (15). Before discussing this result, we stress that Proposition 5
is linked to Proposition 4 and thereby depends on the specific payment rule adopted in
(13) which limits its scope, see Footnote 12. The positive news is that weakly
renegotiation-proof equilibria exist and that the underlying strategies can replace
trigger strategies. Surprisingly, imposing a more restrictive equilibrium concept does not
result in a higher threshold level for the discount factor or a reduced upper bound on
agents 1's bargaining weight. In Appendix B we show that agent 2 obtains exactly his
minmax payoff on his punishment path. Since this is the same payoff as under the trigger
strategies, both strategies employed as punishment strategies are payoff-equivalent to
agent 2. As before, only agent 2 has an incentive to deviate. Given the payoff-equivalent
punishments to agent 2, this must result in the same thresholds as derived under trigger
strategies. We close this section with several remarks on the implications of the penalty
in player 2's punishment path. Note that agent 2's worst RPE payoff consists of his
expected payoff E{b2(e2)} minus a penalty in the first period, which is below his minmax
value, followed by his expected maximum RPE payoff in all future periods, which is above
his minmax value. Although we objected against payoffs below the minmax value in Remark 2,
this argument does not apply here because, by paying the penalty, agent 2 invests in
restoring the cooperation, which might be interpreted as either to repent and show
remorse, or to regain agent 1's trust. Furthermore, the penalty equals the present value
of the entire expected net surplus of all future periods from the second period onwards,
which can be quite substantial. Even though agent 1 receives his minmax payoff in all
future periods from the second period onwards, this agent receives almost the entire
present value of the overall net surplus as the penalty in the first period (he only
misses out on the net surplus of the first period, in which he only receives E{b1(e1)}).
Theoretically, such a substantial penalty is fine, but in practice it might not be
realistic. For practical purposes, one might resort to weights α1 < α0 < α2 that are
closer together and construct paths similar as described above with one exception: the
punishment path for agent 2 specifies (e1, e2) and some small penalty in the first period,
followed by the Nash bargaining agreement α2 for several periods before it continues
forever with Nash bargaining agreement α0 (instead of α1).14 Then, as before, agent 1 has
no incentive to deviate and agent 2 should be given enough incentives to undergo any of
these three paths. We leave this option for future research. The main message of this
section is that Pareto efficient weakly renegotiation-proof equilibria can be derived and
that we characterized its theoretically largest set, which happens to coincide with the
set of sustainable Nash bargaining agreements in SPE.

<h>CONCLUSION</h>
----------

This paper is the first to systematically assess the implications of repeated interaction
for the sustainability of river sharing agreements between riparian neighbors. We obtain
an interesting combination of results. First, our Folk Theorem for river sharing problems
in Proposition 3, further refined in Propositions 4 and 5, provides clear conditions for
sustainable agreements in terms of the distribution of the gains from cooperation.
Remarkably, the complete set of sustainable Nash bargaining agreements under subgame-
perfect equilibrium can also be sustained by the more restrictive weakly renegotiation-
proof equilibrium. Second, in Proposition 2 we establish a trade-off between the
efficiency and stability of agreements, which illustrates the importance of considering
repeated interaction. Repeated interaction tends to favor the downstream agent, which may
seem counterintuitive at first, but may explain empirical observations on downstream
states managing to negotiate a substantial share of upstream river water. Our results
provide non-cooperative support for solutions that assign larger shares of the pie to
downstream agents. At the lowest possible threshold on the discount factor, only the
downstream incremental distribution, proposed by Ambec and Sprumont (2002), that assigns
all gains from cooperation to downstream agents can be sustained and this distribution
remains sustainable for higher discount factors. Finally, the model developed in this
paper offers ample scope for extensions and applications. One obvious extension is to
allow for more general river geographies as in Khmelnitskaya (2010), Ansink and Houba
(2012), or van den Brink et al. (2012). One obvious application is to repeat the analysis
of the Bishkek Treaty in the Aral Sea basin by Ambec et al. (2013) in the dynamic setting
of this paper. Their static analysis showed that actual payments under this agreement
approximate the payment rule induced by the downstream incremental distribution. In a
static setting, this result implies instability. When considering repeated interaction,
however, the results in our paper suggest that this payment rule may actually be well-
chosen.


<h>REFERENCES</h>
----------

  [2] Stefan Ambec, Ariel Dinar, Daene McKinney. Water sharing agreements sustainable to reduced flows. doi:10.1016/j.jeem.2013.06.003
  [3] Stefan Ambec, Yves Sprumont. Sharing a river. doi:10.1006/jeth.2001.2949
  [4] Erik Ansink, Harold Houba. Market power in water markets. doi:10.1016/j.jeem.2011.10.002
  [5] Erik Ansink, Arjan Ruijs. Climate change and the stability of water allocation agreements. doi:10.1007/s10640-008-9190-3
  [6] Erik Ansink, Hans Peter Weikard. Composition properties in the river claims problem. doi:10.1007/s00355-014-0862-3
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  [11] Lynne Lewis Bennett, Charles W. Howe. The interstate river compact: Incentives for noncompliance. doi:10.1029/97WR03384
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<ART>Tax-benefit systems and differences in aggregate labour force participation: Comparative evidence from the Czech Republic and Hungary
================================================================================

Authors: Kamil Galuščák, Gábor Kátay
DOI: 10.1016/j.ecosys.2019.100701
Year: 2019
ASJC codes: 2002
Keywords: Cross-country comparison, Labour supply, Microsimulation, Participation rate, Tax-benefit systems

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This paper investigates the extent to which cross-country differences in aggregate participation rates can be explained by differences in tax-benefit systems. We take the example of two countries, the Czech Republic and Hungary, which – despite a lot of similarities – differ markedly in labour force participation rates. Using comparable individual-level labour supply estimates, we simulate how the aggregate participation rate would change in one country if the other country's tax and social welfare system were adopted. The estimation results for the two countries are quite similar, suggesting that individual preferences are essentially identical in the two countries. The simulation results show that about one-third of the difference in the participation rates of the 15–74 year-old population and more than two-thirds of the participation of the prime-age population can be explained by differences in the tax-benefit systems.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

A cross-country comparison of labour force participation rates is the most straightforward
way to identify labour supply problems in a particular country or set of countries.
International organisations, central banks and economic think-tanks often motivate their
policy recommendations by comparing a country’s participation rate – usually broken down
by selected sub-populations – against an international standard or against other similar
countries’ statistics. The resulting recommendations frequently involve, but are not
limited to, reforms of the country’s tax and welfare system to restore or improve work
incentives.1 That is, the financial incentive to work is implicitly the primary candidate
for explaining cross-country differences in the participation rates of apparently
homogeneous groups of individuals. Is this really the most important factor in explaining
cross-country differences, or are other aspects such as differences in preferences or
other observed and unobserved characteristics (e.g. average health status) even more
important? To what extent can differences in financial incentives explain the observed
differences in labour force participation between countries? Although the impact of labour
taxation and the welfare benefit system on labour force participation has been widely
investigated in the empirical literature, the extent to which cross-country differences in
participation rates can be explained by the diversity of tax-benefit systems has never
been addressed directly. To fill the gap, we take the example of two countries, the Czech
Republic and Hungary. We use, for both countries, a very detailed, complex microsimulation
model and comparable micro estimates of labour supply at the extensive margin (i.e. the
participation decision) to quantify the part of the difference in the two countries’
participation rates accounted for by different tax and welfare benefit systems. More
precisely, we first estimate the same labour supply models for Czech and Hungarian
individual-level data. Two models are tested for both countries: a structural, random
utility labour supply model originally proposed by Van Soest (1995) and a reduced-form
model relating the participation probability to the financial gains from accepting a job.2
The entirely comparable estimated equations for the Czech Republic and Hungary are then
used to simulate how labour supply would change in one country if it adopted the other
country’s tax and social welfare system. Assuming that the economies are supply-driven in
the long run, the initial labour supply shock fully translates into participation and the
results of the simulations can be interpreted as the effect of differences in the tax-
benefit systems on the differences in the two countries’ participation rates. Overall, our
empirical strategy follows a standard procedure in assessing the impact of tax and
transfer system reforms on labour supply at the extensive margin. However, instead of
assessing the effects of a specific past, planned or ad hoc hypothetical reform, we
analyse the labour supply effects of adopting another country’s tax-benefit system. In
doing so, this paper offers the first tentative explanation of cross-country differences
in labour force participation rates by differences in taxation and welfare benefits. The
closest strand of literature uses cross-country individual-level or disaggregated data
either to investigate the labour supply effects of a specific policy change or to explain
developments in participation rates from a cross-country comparative perspective. Some
recent empirical studies analyse the differences in micro- and macro-level elasticities
using cross-country individual-level data (Jäntti et al., 2015); others study the effect
of hypothetical welfare reforms (e.g. Immervoll et al., 2007) or tax reforms (see, for
example, Aaberge et al., 2000, for a cross-country analysis of flat-tax reforms); cross-
country microsimulation models are also used to estimate governments’ redistributive
preferences (Blundell et al., 2009; Bargain et al., 2011). Some other papers use
individual-level or disaggregated data to describe the evolution of labour supply in some
selected countries, either for the whole population (Balleer et al., 2014, or Blundell et
al., 2013) or for a selected sub-population (e.g. Cipollone et al., 2014, for women).
However, none of these or any other existing empirical papers have so far provided direct
evidence to explain differences in participation rates between countries. The Czech
Republic and Hungary provide an interesting case for comparison. The two countries exhibit
a lot of similarities: their economies are geographically close, similar in size and level
of economic development, and partly share a common history. In particular, both economies
experienced full employment until the regime change at the end of the 1980s. Despite all
their common factors, their participation rates differ markedly. In 2008 – the reference
year we use for our simulation – with only 54.3% of the 15–74 year-old population working
or actively seeking employment, Hungary recorded the second lowest participation rate
among EU member states (behind Malta), while the Czech participation rate was close to the
EU15 average (63.1% in the Czech Republic and 64.1% in the EU15, see Section 2.1). The low
Hungarian participation rate is often considered to be the result of a combination of high
taxes on labour and a relatively “generous” transfer system. After describing some
stylised facts about Czech and Hungarian labour force participation and the key
differences between the two countries’ tax and social welfare systems (Section 2), we
present our methodology in Section 3. Our estimation results (presented in Section 4) show
that the labour supply elasticities obtained from the structural and reduced-form models
are quite similar in both countries. Moreover, the estimated labour supply elasticities
for the Czech Republic are very close to the results for Hungary. Overall, the results
suggest that, at least in this dimension, individual preferences are very close in the two
countries. This even holds true for sub-populations depending on age group, level of
education, gender and marital status. In both countries, lower educated people and married
women are the most responsive to tax and transfer changes. Given the large dispersion of
the labour supply elasticities found in the empirical literature for different countries
and time periods, the similarities of the estimated elasticities for the two countries we
analyse using two distinct models are in line with the evidence in Bargain et al. (2014),
suggesting that a considerable part of the cross-country variation in the elasticities
found in the literature is driven by methodological differences. The simulation results
suggest that about one-third of the difference in the participation rates of the 15–74
year-old population and more than two-thirds of the participation of the prime-age
population can be explained by differences in the tax-benefit systems. The results are
quasi-symmetric, meaning that if the Czech system was adopted, the Hungarian participation
rate would increase by about the same number of percentage points as the Czech
participation would decrease if the Hungarian system were implemented. The highest
responses are obtained for individuals with a low level of education and for married
women. These differences are related to the higher personal income taxes for low earners
and the more generous welfare system in general and maternity allowances in particular
that are in place in Hungary as compared to the Czech Republic.

<hs>  Labour force participation in the Czech Republic and Hungary</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The Czech Republic and Hungary share many similarities. Together with Slovakia and Poland,
the four countries of the Visegrád group3 have long been considered frontrunners of the
fundamental systemic transformation from central planning to a market economy following
the collapse of communism in 1989. After an initial recession, widespread changes to their
economic systems shifted these countries to a relatively fast growing path. However, there
are some marked differences in the transition paths they chose to pursue. These particular
differences, together with all the common factors they share (such as their largely
similar history, geographical closeness and the similarities in their initial conditions
before the regime change), make the Visegrád countries a natural subject for comparative
research. Comparing the two countries under investigation in this study, the Czech economy
outperforms the Hungarian economy by a significant margin. By 2008 (the reference year for
our comparison; more on this later), the Czech Republic had reached 76% of the EU15
economic average in terms of GDP per capita (measured in purchasing power standards; see
Table A.1 in Appendix A). The Hungarian economy lags behind with only 56% of the EU15
average. However, the largest part of the difference in relative economic development
between the two countries can be explained by the lower employment rate in Hungary: the
difference between labour productivities, measured as GDP per employed person, is 71% of
the EU15 average in the Czech Republic and 64% in Hungary. The total hourly compensation
of employees is also similar in the two countries, reaching 54% of the EU15 average in the
Czech Republic and 46% in Hungary. The two countries are also close in terms of openness
and economic structure. With export shares of 63% in the Czech Republic and 79% in
Hungary, both economies are remarkably open. The largest share of exports goes to EU
countries, in particular to Germany. The Czech and the Hungarian economies are both
largely industry-oriented, also in comparison to EU15 standards. On the other hand, the
share of public administration in GDP is rather close to the EU15 minimum in both
countries. Despite all the similarities, the participation rates differ markedly in the
two countries. While Hungary lies near the low end among EU countries, the Czech Republic
is around the middle of the ranking (see Fig. 1). This observation holds for both the
working-age and prime-age populations. The significant differences in labour market
performance are typically explained by the different policies adopted during the first few
years of the transition process and kept – at least partly – unchanged since then. Both
countries implemented fast-track reforms in the early 1990s, with two main differences.
First, Hungary opted for case-by-case privatisation as opposed to the voucher
privatisation method adopted by the former Czechoslovakia.4 Second, the Hungarian
government introduced strict bankruptcy regulations in 1992. The differences in
privatisation methods and the draconian bankruptcy regulations implemented in Hungary
provoked a much larger drop in employment in Hungary as compared to Czechoslovakia.
Between 1990 and 1993, total employment declined by 9% in Czechoslovakia and by 22% in
Hungary. Moreover, in Hungary, a number of policy measures – such as alleviated conditions
for entering the old-age or disability pension systems – contributed to pushing people out
of the labour force rather than into unemployment. As a result, the participation rate
declined continuously until 1997, when it was only 50.6% of the 15–74 year-old population,
about 10 percentage points lower than the EU15 average and more than 13 percentage points
lower than in the Czech Republic.5 Table 1 provides additional information by breaking
down the participation rates by selected sub-populations. The participation rates (column
1) and population shares (columns 2–4) are expressed as a percentage of the corresponding
sub-population. The numbers presented in the table are based on the database we use in
this paper, namely the Survey of Income and Living Conditions (SILC) data for the Czech
Republic and the Household Budget Survey (HBS) database for Hungary (see more on the
datasets in Section 4). The total participation rates for the full sample of 15–74 year-
old individuals (row 1, column 1) are somewhat closer in the two countries in our datasets
than in the official data based on the Labour Force Survey (in Fig. 1). This is due to the
fact that our datasets are representative at the household level, while the Labour Force
Surveys are representative at the individual level. The difference of 7 percentage points
is still considerable. The largest difference in participation rates in favour of the
Czech Republic is observed among the youth population (15–24 year-olds, second row). While
the large share of inactive youths can be explained by school attendance, the low share of
youth participation in Hungary is still alarming, all the more so since the share of
youths attending full-time education is also lower in Hungary than in the Czech Republic
(column 2). Among the prime-age group, participation rates are significantly higher in the
Czech Republic for lower-educated individuals, especially for those with elementary school
as the highest level of education, while participation rates are close to each other for
persons with tertiary education. Since lower educated individuals are usually found to be
more responsive to tax and transfer changes (more on this in Section 4), the participation
rates by educational attainment in the two countries are consistent with the higher taxes
and more generous transfer system in Hungary as compared to the Czech Republic (see the
next sub-section). Finally, the elderly population (aged 56 years or older, last row of
Table 1) is considerably less active in the labour market in Hungary than in the Czech
Republic. This divergence is likely to be related to the higher share of old-age and
disability pensioners in Hungary within this population group. While the Hungarian old-age
pension reform in 1997 and the successive strengthening policies adopted in order to
reduce abuse of the disability pension scheme have gradually increased the effective
retirement age and reduced the number of new disability claims granted, the effect of the
policy responses to the transition shock is still visible among the older generation.

<hs>  Key elements of the Czech and Hungarian tax and transfer systems</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The Czech and Hungarian tax-benefit systems are both characterised by individual personal
income taxation and a broad range of welfare benefits. In what follows, we briefly
describe and compare the two systems effective in 2008, the reference year we used for our
simulation.6 In this section, we only look at the main characteristics of the systems that
apply to regular wage earners; the self-employed and other specific cases are not
considered. In our empirical work, more details are taken into consideration. Additional
details on the transfer systems of the two countries are presented in the Appendix. For a
more comprehensive description of the two systems, see, for example, the country chapters
of the OECD’s Benefits and Wages publication.7 In both countries, labour incomes are
subject to personal income tax and employer and employee contributions. In Hungary, the
tax schedule comprises three brackets, with tax rates of 18%, 36% and 40%.8 Employees with
annual earnings under a given threshold are eligible for an earning income tax credit
(EITC) of 18% of their wage income, which is phased out at a rate of 9%. A child tax
credit (fixed amount) is available for families with three or more children. Social
security contributions related to sickness, unemployment and pensions are applied. In the
Czech Republic, family taxation for married couples with children was introduced in 2005.
The joint taxation, however, became irrelevant when a flat tax rate of 15% was introduced
in 2008. It is applied to the so-called super-gross income, which includes employer social
security contributions. Tax credits are available per person, per spouse under a given
income and per dependent child. If the tax credit per child is negative, it is provided to
the household as a tax bonus. Comparing the two personal income tax (PIT) systems, Fig. 2
reveals that, first, the Hungarian system is more progressive and, second, average taxes
are higher. Moreover, the Czech average tax rate can be negative for families with
children if the calculated income tax is lower than the amount of family benefit the
taxpayer is eligible for. The higher average PIT rates in Hungary are also reflected in
higher tax revenues: in 2008 the Hungarian government collected 7.5% of GDP as PIT tax
revenue, compared to 3.5% in the Czech Republic (see Table 2). Both countries provide a
wide range of social benefits in order to – at least partly – compensate for temporary
loss of labour income, to reduce and prevent poverty or to achieve other goals. Overall,
if we look at entitlement periods and the share of GDP spent on various transfers in 2008,
the Hungarian benefit system seems more generous than the Czech one (Table 2). In 2008,
Hungary spent almost twice as much (expressed as a percentage of GDP) on unemployment
benefits and about 60% more on old-age and disability pensions compared to the Czech
Republic. The difference is even greater in the case of maternity allowances, especially
in terms of entitlement period. Although the net amount of the maternity benefit is
usually higher in the Czech Republic during the first 6 months after childbirth, the
entitlement period is much longer in Hungary: conditional on past employment, Hungarian
mothers can receive up to 70% of their previous income until the second birthday of the
youngest child and parents are eligible for a fixed amount until the third birthday of the
youngest child. Even longer entitlement periods apply for the third child, twins and
disabled children. As a general rule, in Hungary, maternity benefits and unemployment
benefits are either fixed amounts or depend on previous income and are subject to income
taxation. On the other hand, other social benefits and pensions are exempt from taxation.
In the Czech Republic, all benefits are non-taxable (except for very high pensions). In
the case of maternity benefits, the amount is calculated based on previous gross income,
whereas unemployment benefits are calculated based on previous net income. These
differences make a direct comparison of the two systems rather challenging. Some details
of the two welfare benefit systems are listed in Table 2. For a more detailed description,
see the Appendix or the references presented in the first paragraph of this section.

<h>METHODOLOGY</h>
-----------

We first estimate, separately for Czech and Hungarian individual-level data, a structural
and a reduced-form labour supply model where both taxes and transfers are treated in a
unified framework. In what follows, we refer to this step as the “estimation part”. In the
second step, the “simulation part”, we use these estimated equations to simulate how each
individual’s probability of being active – and hence the aggregate labour supply – would
change in one country if it adopted the other country’s tax-benefit system. More
precisely, we perform a microsimulation exercise: we replace the net income variables
(wages, transfers and non-labour incomes) in the estimated equations by the values that
would result from adopting the other country’s tax and transfer system. As a consequence
of the benefits gained or losses suffered due to changes in the effective tax rates and
the amount of (potential) transfers, individuals are expected to adjust their labour
supply according to the estimated labour supply equations. The weighted average of the
individual changes in the participation probabilities corresponds to the aggregate labour
supply shock induced by the hypothetical reform. Under certain assumptions detailed below
(see Section 3.4), the result of this exercise reveals the extent to which the difference
between the two countries’ participation rates can be explained by the differences in the
taxation and welfare benefit systems. In this framework, the part of the cross-country
differences in participation rates that can be attributed to the differences in tax and
welfare systems is assessed using counterfactual simulation scenarios. That is, the
effects of the cross-country differences in tax-benefit systems are only indirectly
identified. Ideally, to address this question directly, one would need to observe a
country that adopts the entire tax-benefit system of another country. Such a quasi-
experiment would allow us to use a more transparent identification strategy and to
directly estimate the impact of such a large-scale reform.9 In the absence of such an
experiment, the approach adopted in this paper provides a viable alternative strategy.

<hs>  Modelling labour supply at the extensive margin</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The labour-supply decision is modelled as a discrete choice problem. Originally proposed
by Van Soest (1995), this approach has become increasingly popular and quite standard in
recent years. In this framework, utility-maximising individuals are supposed to choose
between a few alternative discrete sets of hours of work, such as inactivity (zero hours
worked), part-time or full-time. Reducing the maximisation problem to choosing among a
discrete set of possibilities yielding different utilities considerably simplifies the
problem and provides a simple yet rather general way of representing labour supply
decisions in the presence of nonlinear and non-convex budget constraints. The model is in
principle very flexible. The only restriction on the model is the imposition of increasing
monotonicity in consumption. In our empirical work, we model individual labour supply
decisions. Married couples or individuals living with a partner take into account the
labour market status of their husbands, wives or partners, but household members do not
optimise collectively. Furthermore, we assume that there are only two labour-market
states, active and inactive. Indeed, in both the Czech Republic and Hungary, part-time
work is relatively rare: before the outbreak of the crisis, the share of part-time
employees among all workers was less than 5% in both countries. By 2014, this share had
increased to 6.4% in the two countries. For comparison, the average share of part-time
employees in the EU28 reached 18.2% in 2008 and increased further to 20.4% in 2014.10

<hs>  Limitations and interpretation of the simulation results</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Whether the initial labour supply shock induced by the adoption of the other country’s
tax-benefit system fully translates into increased participation (and employment) in the
long run depends on the general equilibrium interactions of the entire economy. Our
approach implicitly assumes a textbook (fully supply-driven) neoclassical general
equilibrium long-run model of a small open economy with perfectly elastic capital supply.
Our results are thus equivalent to the output from the general-equilibrium behavioural
microsimulation model of Benczúr et al. (2018) when perfectly flexible capital supply is
assumed. The perfect flexibility of capital supply is equivalent to assuming the non-
existence of demand-side constraints on the labour market.21 In this framework, the
expected rate of return on capital is pinned down by international benchmarks, which
implies that the capital-to-labour ratio and the ratio of factor prices stay constant in
the long run. It follows that, for example, after a positive labour supply shock induced
by a tax cut, capital accumulation will follow until the new equilibrium is reached with
an unchanged capital-labour ratio. After the adjustment period, gross wages will also
reach their pre-reform level, so factor prices remain unchanged in the long run. The
initial labour supply shock therefore fully translates into participation in the long run.
Consequently, under these assumptions, the results of our simulation exercises can be
interpreted as the effect of differences in the tax-benefit systems in the two countries
on the differences in the two countries’ participation rates.22 While these assumptions
are quite standard in the literature, several factors can realistically impede the
adjustment process. To start with, possible demand-side constraints can prevent the full
adjustment of gross wages, which would limit the labour supply response (if the original
shock comes from the demand side, for example following a decrease in employer
contributions) or increase unemployment rather than employment (for example following a
decrease in PIT or employee contributions, or following a strengthening of the benefit
system). In the latter case, labour force participation is still impacted. However, the
additional mass of unemployed people might give up searching after some time and withdraw
from the labour market because of failed searches (discouraged worker effect). Second,
search-and-matching frictions on the labour market might also impact the results. For
example, although a shortened eligibility for unemployment benefits increases labour
supply and strengthens job-search incentives, it might also affect the successful matching
rate negatively. The overall effect of the shift in the aggregate successful matching rate
is similar to the above-discussed demand-side constraints. Nevertheless, Horvath et al.
(2018) adopt a similar modelling strategy to assess the impact of tax-benefit reforms in
Slovakia and extend it with a search-and-matching block. Their results suggest that
search-and-matching frictions have a limited impact in the long run. On the other hand,
the impact of the tax and transfer reforms may also be higher than predicted by our
simulations. We simulate the effects of adopting the other country’s tax and transfer
system in a static framework. That is, we assume that the tax and transfer system is not
correlated with other observable or unobservable characteristics. In the long run, people
might change all their life decisions in response to a drastic change in the tax and
welfare system. For example, reducing the rate of the labour tax or transfers might make
individuals more inclined to pursue higher education. As a consequence, the composition of
the population might also change following a tax and transfer reform, which might in turn
affect the aggregate participation rate. Finally, the “unexplained” part of the difference
between the two countries’ participation rates is possibly also affected by some elements
of the transfer system that we do not explicitly model, most importantly the differences
in the old-age and disability pension schemes. Although both types of pensions are
included in the model, neither individuals’ retirement decision, nor their access to the
disability pension scheme is taken into account in our microsimulation exercise. That is,
we assume that individuals’ retirement decisions, their access to the disability pension
scheme and the amount of these pensions remain unchanged when the other country’s welfare
benefit system is adopted.

<h>RESULTS</h>
-------

We restrict our analysis to the working-age population of individuals aged 15–74 years,
but use information on the full population to generate the relevant variables, compute net
incomes and generate (hypothetical) transfers.23 The labour supply estimation part is
carried out using Survey of Income and Living Conditions (SILC) data for the Czech
Republic for the years 2005–2010. For the simulation part, explained in detail in Section
3.3, we restrict the sample to the 2008 wave. The SILC is a yearly cross-section survey of
households that provides detailed information on demography and incomes. For each year,
the survey contains broadly 10,000 households and 23,000 individuals. All income variables
(labour and non-labour incomes, transfers) are expressed in total annual terms. To compute
net incomes and potential transfers that individuals are entitled to or would be entitled
to in the absence of any income from work, we used a modified version of the tax-benefit
model developed by Galuščák and Pavel (2012). We used the same codes to compute net labour
incomes, but extended the original version of the model in order to take into account more
complex features of the Czech tax and transfer system (e.g. taxes on capital revenues and
maternity benefit). As for the transfers, we simulated the total annual amount of benefits
the individual gets if he is not working or could get if he decided to stop working.24 To
compute net incomes and hypothetical transfers for Hungary, we use the microsimulation
model developed by Benczúr et al. (2018).25 The model features a very detailed static
fiscal microsimulation model, combined with behavioural labour supply responses at both
the intensive and the extensive margin and a small neoclassical macro model.26 The fiscal
microsimulation model is parameterised for each year since 1998. The estimation part is
carried out using all waves between 1998 and 2008, while the simulation part (see Section
3.3) uses only the 2008 wave. The Hungarian model runs on the Household Budget Survey
(HBS) database, which is more detailed but otherwise comparable to the CZ-SILC database.
The difference with respect to the CZ-SILC is twofold: first, several income variables in
the Czech database are broken down into several categories in its Hungarian counterpart;
second, some variables – such as income from abroad, income of minors, life annuity
payments, scholar grants and severance indemnities – are reported in the Hungarian
database but no information is available from the Czech database. Finally, we carefully
linked all the variables to their counterparts in the other database. If one-to-one
correspondence could not be achieved, the closest possible several-to-one match was
established (see Tables C.1 and C.2 in the Appendix).

<hs>  Estimation results</hs>
  ~~~~~~~~~~~~~~~~~~

Table 3 reports the estimated conditional marginal effects evaluated at the population
averages and by selected subgroups following the methodology presented in Sections 3.1 and
3.2. As expected, a higher net wage increases the probability of participation in the
labour market, while means-tested transfers have the opposite effect. Overall, the
structural models provide very similar conditional marginal effects to the reduced-form
models and the Czech results are remarkably close to the Hungarian ones. For the whole
population, the lowest wage elasticity is obtained for the Czech Republic with the
structural model and the highest elasticity is obtained with the structural model for
Hungary. On average, a 10% increase in the net wage leads to a 2.4–2.8 percentage point
increase in the probability of being active in the Czech Republic and a 2.8–3.4 percentage
point increase in Hungary. The estimated marginal effects of the transfers are even closer
to each other across countries and model specifications. The effect of a 10% increase in
transfers on the average individual’s probability of being active ranges from -0.9
percentage points in Hungary according to the reduced-form model to -1.2 percentage points
in the Czech Republic with the structural model. The similarity of the results suggests
that, on average, individual preferences are essentially identical in the two countries.
This is also true for selected subgroups depending on age group, level of education,
gender and marital status. Again, the structural models basically imply the same net wage
and transfer elasticities as the reduced-form models and the Czech results are very close
to the Hungarian ones. The conditional marginal effects calculated on the prime-age
population averages (25–54 year-olds) are lower (in absolute value) than the results for
the whole population, indicating that prime-age individuals are less responsive to tax and
transfer changes than the rest of the population. Within the prime-age population,
however, the education level strongly influences individuals’ responsiveness: the lower
educated (“elementary school or less”), probably highly transfer-dependent group, is
highly responsive, while the estimated elasticities for secondary and tertiary educated
people are much smaller. The remaining rows in Table 3 suggest that women’s participation
is more responsive than that of men, particularly for married women. The estimation
results and the implied wage elasticities are qualitatively in line with existing results
in the empirical literature. However, a direct comparison of the elasticities is not
straightforward. There is a large consensus in the literature that women (and especially
married women) respond more to changes in their net market wage than men. Lower educated
individuals are also usually found to be more responsive than the average. The variation
in the magnitude of the estimated labour supply elasticities found in the literature is
nonetheless considerable and the reported elasticities are rarely directly comparable for
several reasons. First, with some exceptions, early labour supply models using the
continuous Hausman approach usually do not distinguish between the decision to participate
(the extensive margin) and the decision regarding hours worked (the intensive margin) and
only report uncompensated and/or compensated (Hicksian) hours elasticities, not the
participation elasticity.27 Second, although the discrete choice approach by construction
always includes participation elasticity, estimates from various studies are not easily
comparable due to differences in specifications and definitions. A comprehensive
comparison of the international evidence on labour supply elasticities by Bargain and
Peichl (2013) shows that the large variance in the reported elasticities is – at least
partly – explained by differences in specifications (most importantly, whether wages are
predicted for all individuals or only for non-workers) and the time period considered. A
meta-analysis by Chetty et al. (2013) provides a “consensus” elasticity: according to the
authors, existing micro and macro evidence points towards an aggregate steady-state
elasticity of labour supply at the extensive margin of 0.25. Overall, the marginal effects
obtained for the Czech Republic and Hungary lie in the (rather large) range obtained in
previous studies, especially studies using the discrete choice approach.28 Given the large
dispersion of the labour supply elasticities estimated for different countries and time
periods and using various methodologies, the similarities of the results we obtain for two
different countries is in itself interesting and we tentatively suggest that
methodological differences might be responsible for a considerable part of the cross-
country variation in the elasticities found in the literature. The findings of Bargain et
al. (2014), who estimate a comparable labour supply equation for a large set of countries
and show that cross-country differences in genuine work preferences are rather small,
corroborate this view.

<hs>  Simulation results</hs>
  ~~~~~~~~~~~~~~~~~~

The simulations were carried out as explained in Section 3.3. The results are shown in
Table 4. The reported figures indicate the participation rates for 2008 (the reference
year chosen for our simulations) for both countries on the overall sample of individuals
aged 15–74 (row (a)) and for the prime-age subsample (rows (b) to (i)). The participation
rates are considerably higher in the Czech Republic than in Hungary for almost all
subgroups (see columns (1) and (6)). The difference in participation rates for the whole
population is 7.0 percentage points according to our datasets. The simulation results
using each country’s own tax and benefit systems are presented in columns (2), (3), (7)
and (8). The reported numbers are weighted averages of the participation probabilities
predicted by the estimated structural equations (columns (2) and (7)) and the reduced-form
equations (columns (3) and (8)). As mentioned in Section 3.3, the constant terms in both
the structural and the reduced-form equations are set so as to match the aggregate
statistics. The simulated full-sample aggregate participations (cells (a2), (a3), (a7) and
(a8)) are therefore equal to the observed participation rates (cells (a1) and (a6)). The
differences in the participation rates for the selected subgroups come from differences in
preferences (captured by the labour supply controls and taste shifters in the logit
equations), differences in productivity and thus in gross wages, differences in average
tax rates, which influence net wages, and/or differences in potential transfers. For both
countries and both models, the simulated participation rates for the selected subgroups
are close to the observed ones. This suggests that, overall, the estimated equations
capture individuals’ heterogeneity quite well. In columns (4), (5), (9) and (10) we show
how Czech and Hungarian labour force participation would change (in percentage points) if
one country adopted the other country’s tax-benefit system. The results of our simulation
exercise show that, overall, the Czech participation rate would decrease by 2.2 or 3.0
percentage points (depending on the model used) if the country adopted the Hungarian
system. The Hungarian participation rate would increase by 2.4–2.5 percentage points if
the Czech system were adopted. These results are close to symmetric and indicate that the
differences in the two tax-benefit systems explain about one-third of the total difference
in the two countries’ participation rates. On average, the difference is even greater for
prime-age individuals, reaching (-2.6)–(-2.8) percentage points for the Czech and 3.0–3.3
percentage points for the Hungarian data (see row (b)). That is, according to our results,
more than two-thirds of the total difference in participation rates for the prime-age
population between the two countries can be explained by the differences in the tax-
benefit systems. The simulation results remain broadly symmetric for most of the selected
subgroups.29 The highest response is obtained for low-educated individuals and for married
women. The large response of these subgroups is most probably related to the higher
personal income taxes for low earners and the very generous maternity benefit system in
place in Hungary as compared to the Czech Republic (see Section 2.2). Overall, our results
suggest that the major part of the differences in the participation rates for prime-age
individuals is related to the tax and transfer systems. Assuming that the hypothetical tax
and transfer reform of adopting the Czech system does not alter the composition of the
Hungarian workforce and no demand-side constraints prevent adjustment (see Section 3.4 for
a discussion of these possibilities), some additional measures would need to be
implemented in Hungary for it to reach the Czech participation rate for 25–54 year-olds.
This could be achieved, for example, by introducing a lower 5% PIT bracket up to the
minimum wage or by shortening the eligibility for unemployment benefits by one month
(without touching the longer entitlement period for the elderly), but other measures could
also be considered. On the other hand, the gap for the whole working-age population is too
large for Hungary to realistically reach the Czech participation rate level by re-
parametrising the part of the tax-benefit system that we model explicitly. The
“unexplained” part of the difference between the two countries’ participation rates is
most likely largely affected by some other elements of the transfer system, most
importantly the differences in the oldage and disability pension schemes (see Section 3.4
for a discussion of how these two transfer types are taken into account in our
simulations). Although several restrictive measures have been adopted in Hungary to reduce
abuse of the disability pension scheme and increase the effective retirement age, the
shares of early-retired and disabled individuals are still relatively high in Hungary by
international comparison (see Table 1).

<h>CONCLUSION</h>
----------

Taking the example of two countries, the Czech Republic and Hungary, this paper
investigates the extent to which cross-country differences in aggregate participation
rates can be explained by the disparities in their tax-benefit systems. We first estimate
the same structural and reduced-form labour supply models for Czech and Hungarian
individual-level data and use comparable estimates of labour supply at the extensive
margin to simulate how the aggregate participation rate would change in one country if it
adopted the other country’s tax and social welfare system. Our estimation results yield
similar labour supply elasticities for both the structural model and the reduced-form
model and for both countries, suggesting that individual preferences are essentially
identical in the two countries analysed. Consistently with previous findings, lower
educated individuals and married women are the most responsive to tax and transfer
changes. The simulation results show that about 2.2–3.0 percentage points out of the total
difference of 7.0 percentage points – i.e. about one-third of the total difference – in
the participation rates of the 15–74 year-old population can be explained by differences
in the tax-benefit systems. The explained part is higher for prime-age individuals: for
this group, more than two-thirds of the total difference in participation rates is related
to differences in the tax-benefit systems. The simulated effects are quasi-symmetric for
almost all subgroups, meaning that if the Czech system was adopted, the Hungarian
participation rate of a specific subgroup would increase by about the same number of
percentage points as the Czech participation rate would decrease if the Hungarian system
were implemented. The largest difference explained by the differences in the tax-benefit
systems is identified for low-educated individuals and for married women. These
differences are related to the higher personal income taxes for low earners and the more
generous welfare system in general and maternity allowances in particular in place in
Hungary as compared to the Czech Republic. The “unexplained” part of the difference is
also likely to be affected by some elements of the transfer system that we do not
explicitly control for, most importantly the differences in the old-age and disability
pension schemes. Moreover, in the long run, the tax and transfer system might also
influence individuals’ schooling or other life decisions, which might affect the aggregate
participation rate through the changing composition of the population. Obviously, these
results cannot be directly generalised to other countries. First, it is possible that
individual preferences differ more across countries with different cultural and historical
backgrounds or institutional structures even within narrowly defined sub-populations.
Second, cross-country differences in the composition of the working-age population may
lead to different results even following a similar shock to net income levels.
Nevertheless, the exercise presented in this paper sheds some light on how important the
tax-benefit system can be in explaining the differences in labour force participation
between two otherwise similar countries. Finally, it is important to note that we do not
suggest that Hungary should adopt the Czech tax and transfer system in order to increase
labour force participation. First, even though the Czech participation rate is close to
the EU15 average (the usual benchmark for emerging EU member states), the Czech system
might not be optimal in every respect. Second, governments’ redistributive preferences may
be different and therefore the optimal policy may also differ. Third, given the country’s
fiscal constraints, it may not be optimal for Hungary to implement such a large-scale tax-
benefit reform. Relative to the 2008 situation, the fiscal impact of implementing the
Czech system would be considerable: assuming a constant average consumption share (84%),
the reform would impact the budget by 4% of GDP. This is almost double the fiscal impact
of the tax and transfer reforms implemented in Hungary between 2008 and 2010, which can
already be considered very large (see Benczúr et al., 2018). Moreover, the effectiveness
of the reform largely depends on the additional measures chosen to cover the budget
deficit. Despite these concerns, the Czech system is still a good benchmark for Hungary,
as it provides a realistically achievable alternative for Hungarian policymakers.

<h>FUNDING</h>
-------

This study was funded by the European Commission, Joint Research Centre; and the Czech
National Bank Research Project No. D1/12.


<h>REFERENCES</h>
----------

  [1] Rolf Aaberge, Ugo Colombino, Steinar Strøm. Labor supply responses and welfare effects from replacing current tax rules by a flat tax: Empirical evidence from Italy, Norway and Sweden. doi:10.1007/s001480050153
  [2] Almut Balleer, Ramon Gomez-Salvador, Jarkko Turunen. Labour force participation across Europe: A cohort-based analysis. doi:10.1007/s00181-013-0716-3
  [5] Olivier Bargain, Kristian Orsini, Andreas Peichl. Comparing labor supply elasticities in Europe and the United States: New results. doi:10.3368/jhr.49.3.723
  [6] Péter Benczúr, Gábor Kátay, Áron Kiss. Assessing the economic and social impact of tax and benefit reforms: A general-equilibrium microsimulation approach applied to Hungary. doi:10.1016/j.econmod.2018.06.016
  [7] Richard Blundell, Antoine Bozio, Guy Laroque. Extensive and intensive margins of labour supply: Work and working hours in the US, the UK and France. doi:10.1111/j.1475-5890.2013.00175.x
  [8] Richard Blundell, Mike Brewer, Peter Haan, Andrew Shephard. Optimal income taxation of lone mothers: An empirical comparison of the UK and Germany. doi:10.1111/j.1468-0297.2008.02261.x
  [9] Raj Chetty, Adam Guren, Day Manoli, Andrea Weber. Does indivisible labor explain the difference between micro and macro elasticities? A meta-analysis of extensive margin elasticities. doi:10.1086/669170
  [10] Angela Cipollone, Eleonora Patacchini, Giovanna Vallanti. Female labour market participation in Europe: novel evidence on trends and shaping factors. doi:10.1186/2193-9012-3-18
  [11] Kamil Galuščák, Jan Pavel. Taxes and benefits: Work incentive Effects of Policies
  [14] Herwig Immervoll, Henrik Jacobsen Kleven, Claus Thustrup Kreiner, Emmanuel Saez. Welfare reform in European countries: A microsimulation analysis. doi:10.1111/j.1468-0297.2007.02000.x
  [15] Markus Jäntti, Jukka Pirttilä, Håkan Selin. Estimating labour supply elasticities based on cross-country micro data: A bridge between micro and macro estimates?. doi:10.1016/j.jpubeco.2014.12.006
<ART>Tests of the co-integration rank in VAR models in the presence of a possible break in trend at an unknown point
================================================================================

Authors: David Harris, Stephen J. Leybourne, A. M.Robert Taylor
DOI: 10.1016/j.jeconom.2016.02.010
Year: 2016  |  Pages: 451-467
ASJC codes: 2002
Keywords: Break point estimation, Co-integration rank, Error-correction model, Information criteria, Trend break, Vector autoregression

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

In this paper we consider the problem of testing for the co-integration rank of a vector autoregressive process in the case where a trend break may potentially be present in the data. It is known that un-modelled trend breaks can result in tests which are incorrectly sized under the null hypothesis and inconsistent under the alternative hypothesis. Extant procedures in this literature have attempted to solve this inference problem but require the practitioner to either assume that the trend break date is known or to assume that any trend break cannot occur under the co-integration rank null hypothesis being tested. These procedures also assume the autoregressive lag length is known to the practitioner. All of these assumptions would seem unreasonable in practice. Moreover in each of these strands of the literature there is also a presumption in calculating the tests that a trend break is known to have happened. This can lead to a substantial loss in finite sample power in the case where a trend break does not in fact occur. Using information criteria based methods to select both the autoregressive lag order and to choose between the trend break and no trend break models, using a consistent estimate of the break fraction in the context of the former, we develop a number of procedures which deliver asymptotically correctly sized and consistent tests of the co-integration rank regardless of whether a trend break is present in the data or not. By selecting the no break model when no trend break is present, these procedures also avoid the potentially large power losses associated with the extant procedures in such cases.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Macroeconomic series are typically characterised by piecewise linear (or broken) trend
functions; see, inter alia, Stock and Watson (1996, 1999, 2005) and Perron and Zhu (2005).
Such breaks in the trend function might occur following a period of major economic
upheaval or a political regime change. In the univariate setting this has spurred a large
literature on testing for an autoregressive unit root when a trend break may be present in
the data. The first proper theoretical treatment of this problem was given by Perron
(1989) who showed that unit root tests which fail to account for a trend break present in
the data have non-pivotal limiting null distributions and are inconsistent under stable
root alternatives. Assuming the putative break date to be known, Perron (1989) proposed
new unit root tests which avoid these problems by modelling the trend break. However, if a
break does not occur this approach loses considerable finite sample power through the
inclusion of an unnecessary trend break regressor. Subsequent approaches have focussed on
the case where the break date is unknown. Zivot and Andrews (1992) base a test on the most
negative of a sequence, taken across all possible break dates, of the Perron (1989)
statistics, while Perron (1997) first estimates the trend break location and then uses the
Perron (1989) test for the estimated break date. The limiting distributions of the Zivot
and Andrews (1992) tests depend on the magnitude of the trend break parameter which
renders them infeasible in practice. The Perron (1997) approach is also problematic in
that the break point estimator has a non-degenerate limit distribution when no break is
present, with the result that the associated unit root test has a different large sample
null distribution vis-à-vis the case where a trend break is present. Size-controlled
inference can then only be achieved by using so-called conservative critical values
corresponding to the case where no break is present, with an associated loss of efficiency
where a break is present. As a result, Carrion-i-Silvestre et al. (2009),  Harris et al.
(2009) and Kim and Perron (2009) advocate approaches based on the use of pre-tests for the
presence of a trend break. In the vector time series setting, un-modelled trend breaks
cause similar problems for the co-integration rank tests of Johansen (1995). For example,
Inoue (1999) documents large losses in finite sample power with the standard trace and
maximum eigenvalue tests of Johansen (1995) when an un-modelled trend break is present in
the data. As we will show in the simulation results we report in this paper, an un-
modelled trend break also causes substantial over-sizing in the standard rank tests,
consistent with the findings for standard unit root tests in Perron (1989). Surprisingly
then, the literature on testing for co-integration rank in the presence of breaks in the
deterministic trend function is relatively sparse compared to the univariate case. In the
context of co-integration rank tests of the type considered in Johansen (1995),  Johansen
et al. (2000) develop likelihood ratio tests, analogous to those considered in the
univariate case in Perron (1989), for the case where the break in the trend function
occurs at a known point. Like Perron (1989) they consider both level break and trend break
models, and extend to allow for multiple breaks in the trend function. Saikkonen and
Lütkepohl (2000) for a level break (but no trend break) at a known date, Lütkepohl et al.
(2004) for a level break (no trend break) at an unknown point, and Trenkler et al. (2007)
for a trend break at a known date, propose further co-integration rank tests, in each case
using the pseudo-GLS de-trending method outlined in Saikkonen and Lütkepohl (2000). All of
these procedures assume that the autoregressive lag length is known to the practitioner.
The approaches taken in the last three of these papers also differ from the approach taken
in Johansen et al. (2000) according to how the data generating process [DGP] under
consideration is constructed. While they adopt a components DGP, forming the observed
process as the sum of the deterministic variables and an indeterministic vector
autoregressive [VAR] process, Johansen et al. (2000), follow Johansen (1995) and place the
deterministic variables directly into the VAR equation. Finally, Inoue (1999), who also
assumes a known autoregressive lag order, develops Zivot and Andrews (1992) type co-
integration rank tests by calculating with-break implementations of the Johansen (1995)
tests over all possible break dates and basing a test on the most positive of these. The
aim of this paper is to address these drawbacks with the existing tests in the literature.
In order to focus attention on what we believe to be the empirically most relevant case,
we follow Trenkler et al. (2007) and consider only the leading example of the trend break
case, but allowing for the possibility of a simultaneous level break. We propose new
testing procedures which in spirit generalise the approach taken by Carrion-i-Silvestre et
al. (2009),  Harris et al. (2009) and Kim and Perron (2009) to the setting of testing for
co-integration rank. We consider two possible approaches depending on whether the
deterministic component is included additively as in Trenkler et al. (2007) or directly
into the co-integrated vector autoregressive [VAR] equation as in Johansen et al. (2000).
In either case the first step in the procedure is based on the use of a consistent
estimator of the break date. In the context of the component DGP of Trenkler et al.
(2007), a multivariate generalisation of the first difference trend break estimator used
in Harris et al. (2009) is proposed, along with a corresponding estimator obtained from
the levels of the data, while for the Johansen et al. (2000) set-up a maximum likelihood
estimator of the break date is used. Based on these break date estimators, for each of the
two approaches an information-based method using a Schwarz (1978)-type criterion is then
employed to select between the version of the model which includes a trend break (included
at the relevant estimated break date) and that which does not. Each of the proposed
procedures also employs a Schwarz-type criterion to select the autoregressive lag length.
Conventional trace-type co-integration rank tests are then computed appropriate to the
model selected by these Schwarz-type criteria. For each of the proposed procedures we
establish that: (i) the estimator of the break fraction is consistent for the true break
fraction; (ii) the information-based methods based on this estimator consistently select
between the with-break and without-break variants of the model, and (iii) the resulting
trace tests can be validly compared to known break date critical values in trend break
case and to the without break critical values in the no break case. A consequence of our
results is that, at least in large samples, the information-based methods we propose allow
us to correctly identify whether we need to allow for a trend break in the model or not.
This then implies that where a break is not present we will not see the loss in efficiency
that is incurred by including a redundant trend break regressor in the model, and at the
same time where a trend break is present we will not see the potentially large impact on
the size and power properties of the rank tests that result from omitting the trend break.
We present Monte Carlo simulation evidence which suggests that the procedure based on the
Johansen et al. (2000) set-up is preferred and generally works very well even for a
relatively small sample size such that the finite sample performance of this procedure is
quite close to that seen for the benchmark rank tests which would obtain with knowledge of
whether a trend break was present or not. The key findings of our Monte Carlo simulation
exercise are presented here, while a more detailed set of results can be found in the
accompanying supplement, Harris et al. (2015).

<h>CO-INTEGRATION RANK TEST PROCEDURES</h>
-----------------------------------

As discussed in the previous section, we now explore general approaches suggested by the
structures of each of (1)–(3).

<hs>  The SC-VECM procedure</hs>
  ~~~~~~~~~~~~~~~~~~~~~

The SC-VECM procedure can then be described as follows.

<hs>  The SC-DIFF procedure</hs>
  ~~~~~~~~~~~~~~~~~~~~~

The SC-DIFF procedure can then be described as follows.

<hs>  The SC-VAR procedure</hs>
  ~~~~~~~~~~~~~~~~~~~~

The SC-VAR procedure is as follows.

<h>ASYMPTOTIC ANALYSIS</h>
-------------------

Some remarks are in order.

<hs>  Simulation design</hs>
  ~~~~~~~~~~~~~~~~~

The tables of results given here are selected to illustrate the important features of the
finite sample properties of the procedures. Nevertheless space constraints mean that
results of the full experiment cannot be reported here, but they are made available in the
accompanying supplement, Harris et al. (2015). Those results help to explain choices made
in the reporting here. For example Tables 2–5 do not include results for SC-VAR because
these tests were found to suffer from substantial size distortions when compared to SC-
VECM and SC-DIFF, but results for SC-VAR are given in Harris et al. (2015). The supplement
also provides finite sample evidence for the choice of 2 as the penalty for the break
fraction parameter, rather than the usual 1.

<h>CONCLUSIONS</h>
-----------

We have focussed on the problem of testing for the co-integration rank in VAR processes of
unknown lag order when a break in the deterministic trend component may be present at an
unknown point in the sample. In order to simultaneously avoid the size and power problems
which can result, even in large samples, from an un-modelled trend break and at the same
time guard against the loss of finite sample efficiency which results from allowing for a
trend break when no trend break is present, we have outlined an approach based on the use
of information criteria. These criteria are used to select the autoregressive lag length
and to select between the trend break and no trend break models, using a consistent
estimate of the break fraction in the former case. Two possible frameworks were considered
depending on whether the deterministic component was included additively in a components
representation or directly into the VAR equation, the latter referred to here as the SC-
VECM procedure. In each case these procedures were shown to deliver asymptotically
correctly sized and consistent tests of the co-integration rank regardless of whether a
trend break is present in the data or not. By selecting the no break model when no trend
break is present, these procedures were also shown to avoid the potentially large power
losses associated with tests which assume that a trend break is known to have occurred,
when in fact no break is present. Monte Carlo simulation results were presented which
suggest that the procedures generally performed well in practice with the SC-VECM
procedure preferred overall.


<h>REFERENCES</h>
----------

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  [10] Søren Johansen. DETERMINATION OF COINTEGRATION RANK IN THE PRESENCE OF A LINEAR TREND. doi:10.1111/j.1468-0084.1992.tb00008.x
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<ART>The economic contribution of the “C” in ICT: Evidence from OECD countries
=========================================================================

Authors: Peter Goodridge, Jonathan Haskel, Harald Edquist
DOI: 10.1016/j.jce.2019.07.001
Year: 2019  |  Pages: 867-880
ASJC codes: 2002
Keywords: Capital, Growth, Growth-accounting, Investment, Prices, Productivity, Telecommunications

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Numerous studies have documented the contribution of ICT to growth. Less has been done on the contribution of communications technology, the “C” in ICT. We construct an international dataset of fourteen OECD countries and present contributions to growth for each ICT asset (IT hardware, CT equipment and software) using alternative ICT deflators. Using each country's deflator we find that the contribution of CT capital deepening to productivity growth is lower in the EU than the US. Thus we ask: is that lower contribution due to a lower rate of CT investment or differing sources and methods for measurement of price change? We find that: (a) there are still considerable disparities in measures of ICT price change across countries; (b) in terms of growth-accounting, price harmonisation has a greater impact on the measured contributions of IT hardware and software in the EU relative to the US, than that of CT equipment; over 1996–2013, harmonising investment prices explains just 15% of the gap in the EU CT contribution relative to the US, compared to 25% for IT hardware; (c) over 1996–2013, CT capital deepening accounted for 0.11% pa (6% as a share) of labour productivity growth (LPG) in the US, compared to 0.03% pa (2.5% of LPG) in the EU-13 when using national accounts deflators; and (d) using OECD harmonised deflators, the figure for the EU-13 is raised to 0.04% pa (4% of LPG).

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Numerous studies have sought to estimate the contribution of ICT to economic growth.
Within the field of growth-accounting, studies include those from EUKLEMS (O’Mahony and
Timmer, 2009; Van Ark and Inklaar, 2005) and earlier work from Oulton (2002) and Jorgenson
(2001) for the UK and US respectively. Those studies showed that: first, in periods of
fast technical change, price indices that do not correct for quality potentially (vastly)
understate growth in real investment and capital services (Triplett, 2004); and second,
better estimation of the ICT contribution requires separating out ICT equipment from plant
& machinery in the estimation of capital services.12 However, in general, the growth
contribution of the “C” in ICT has received less attention than the larger contributions
of IT hardware and software (OECD, 2008). When we consider the role and ubiquity of the
internet in business activity, this is potentially important. Papers that have studied and
considered CT equipment as a distinct asset include (but are not limited to): Oliner and
Sichel (2000), Doms (2005), Corrado (2011b), and Byrne and Corrado (2015). We construct an
international dataset including the US and thirteen European economies to study the growth
contribution of ICT with a particular focus on telecommunications (CT) capital. We treat
all three types of ICT capital (i.e. IT hardware equipment, CT equipment and software) as
distinct assets and use these data to review growth-accounting estimates for Europe
relative to the US. In doing so, we first apply ICT investment deflators from each
country’s national accounts as a benchmark. For all types of ICT capital, we find lower
growth contributions in Europe than in the US. Thus we ask: “To what extent is the smaller
contribution of telecommunications capital deepening in Europe due to: a) inconsistencies
in the measurement of prices for tradeable goods; or b) a lower rate of real (current and
past) CT investment?” To answer this we compare results with those based on sets of
harmonised deflators constructed by the OECD (Schreyer and Colecchia, 2002).3 The
harmonised deflators incorporate some explicit quality adjustment and tend to fall at a
faster rate than those from European NSIs, which are typically not constructed using
hedonic methods.4 We estimate the contribution of CT capital deepening to be positive for
all countries and time periods studied and in the range of zero to 0.24% pa.5 In general,
the CT contribution was higher in the late 1990s and early 2000s but has since declined.
Applying national accounts deflators, CT capital deepening accounted for growth of 0.03%
pa in the EU-13 in 1996–2013, compared to 0.11% pa in the US. Price harmonisation raises
the EU contribution to 0.04% pa, implying that only a small proportion of the difference
relative to the US is explained by inconsistencies in measures of price change for what
are tradeable goods. Instead, the lower EU contribution is explained by weaker growth in
CT capital services and a smaller income share, which in turn are driven by the rate of CT
investment and the level of the real CT capital stock. The rest of this paper is set out
as follows. Section 2 sets out the framework. Section 3 describes features of our dataset
and its construction. Section 4 presents our results and finally, Section 5 concludes.

<h>FRAMEWORK AND EXISTING LITERATURE</h>
---------------------------------

We conduct a sources of growth decomposition for fourteen OECD economies including the US
and thirteen European countries.6 The underlying model is set out below.

        “Aggregation”

        In addition to our analysis by country, we also present (share-)weighted averages
        for country groups11 The relation between individual countries and higher-level
        groups is as follows. Real GDP in the (synthetic) country group grows as in (1)
        but where the shares for K and L are shares in the aggregate. Or put another way,
        all components of (1) can be presented as share-weighted averages using that
        country’s share in the nominal value-added of the group as weights:12 This
        technique creates a weighted average for the country group. Note that a strict
        aggregation would require detailed data on internal trade within the EU (or
        country group) and between the EU (or group) and the rest of the world (RoW).

<hs>  Existing literature</hs>
  ~~~~~~~~~~~~~~~~~~~

This paper is related to a number of strands in the literature. First, a number of
researchers have sought to document the contribution of ICT to growth. Earlier studies
include those from Jorgenson and Stiroh (2000) and Jorgenson (2001) for the US and Oulton
(2002) for the UK, who showed that rapid decline in the prices of semiconductors and ICT
capital was enabling a wave of improved productivity growth. Second, other studies have
looked to make international comparisons of productivity growth and the contribution of
ICT capital. For instance, Van Ark and Inklaar (2005) study the ICT contribution across
countries using the EUKLEMS dataset (O’Mahony and Timmer, 2009) which includes harmonised
constant-quality price indices for IT equipment (but not CT equipment or software). Other
research to consider the deflation of ICT output and its effect on international
comparisons includes (Wyckoff, 1995), which concludes that international variation in
estimated price change (and therefore output) is largely due to methodological differences
rather than real economic phenomena. Schreyer and Colecchia (2002) consider the deflation
of ICT investment and construct harmonised deflators for all three types of ICT capital.
They find that applying harmonised indices raises real growth in ICT investment and
capital services in countries that do (did) not explicitly adjust for quality change.
Similarly, Jalava and Pohjola (2008) use US investment price data for IT and CT equipment
to re-estimate ICT contributions for Finland. Third, a more recent strand of the
literature has sought to improve measurement of CT prices using US data. Doms (2005) and
Corrado (2011a) and Byrne and Corrado (2015) each form new estimates of price change for
CT equipment but do not conduct growth-accounting. Finally, our paper is also related to a
new stream of literature that has sought to better estimate the growth contribution of
telecommunications technology using improved measures of prices and capital services.
Corrado and Jäger (2014) undertake a sources of growth analysis including CT capital and
incorporating utilisation and network effects. Byrne et al. (2017) estimate price change
for (constant-quality) ICT services provided via cloud computing and consider the
implications of fast growing ICT inputs via the cloud (Byrne and Corrado, 2016), which
current national accounting methods may not well measure. Work by Byrne and Sichel (2017)
considers the impact of price mismeasurement in the high-tech sector and implications for
productivity analysis.

<h>DATA</h>
----

The dataset was built primarily from country-level total economy national accounts data
downloaded from OECD.Stat. As documented in the Appendix, where data were incomplete they
were supplemented with other sources with some extrapolation or imputation where
necessary.

<hs>  Time period</hs>
  ~~~~~~~~~~~

For most countries our data run from 1990 to 2013 but for others the data start later. We
therefore conduct most of the analysis over 1996–2013 so that all countries are included
and all country groups are balanced.13

<hs>  Output and gross fixed capital formation (GFCF)</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

For output, we use national accounts data on total economy nominal and real gross value
added (GVA) at basic prices. Gross fixed capital formation (GFCF) data are nominal and
real GFCF in intellectual property products (IPPs, that is: R&D; software; mineral
exploration; and artistic originals; with GFCF in the latter two assets combined),
computer hardware (IT), telecommunications equipment (CT), other plant and machinery (p),
vehicles (v) and (non-residential) buildings (b).14 All specific adjustments to fill in
incomplete data are set out in and below Appendix Table 4.15 On ICT investment, we note
that measurement issues may exist in cases where different aspects of ICT capital are
bundled in the same purchase. In the case of hardware, we note that the convention is that
where software is bundled with hardware, and the values cannot be separated, then the
investment transaction is recorded in hardware. We assume that the same applies to
communications equipment, and that where software is bundled with CT and the values cannot
be separated, then the transaction is recorded in CT equipment. Where CT is bundled with
IT, we assume the transaction is recorded under IT hardware. However, we note the
potential for practice to vary by country, with different countries potentially applying
different methods and varying degrees of effort in unbundling various aspects of ICT
investment. In Fig. 1 we document nominal GFCF in CT equipment across countries. To ease
comparison, estimates are converted to US dollars (USD) using OECD purchasing power parity
(PPP) data.16 As expected, nominal CT investment is highest in the US at $102.4bn in 2013.
Strikingly, the sum of CT investment in the EU-13 in 2013 is substantially less, at
$42.7bn.17 From Fig. 1 we see that, for most countries, nominal CT investment grew
relatively strongly in the late 1990s and/or early 2000s but has since slowed or declined.
Fig. 2 presents indices (2000=1) of nominal investment (in USD), for the US and EU-13, in:
tangible capital excluding ICT equipment (“Tang excl ICT”); intangible capital as defined
in the national accounts (“NA Intang”, that is, software, mineral exploration, artistic
originals and R&D); IT hardware (“IT”); and communications equipment (“CT”). Prior to 2000
(95-00), nominal investment growth in CT equipment was almost twice as fast in the US
(13.2% pa) than the EU-13 (7.7% pa). In the2000′s, prior to the financial crisis (00–07),
growth in GFCF in CT equipment turned negative, at -1.8% pa in the US and -2% pa in the
EU. In the recession and post recession period (07–13), GFCF CT equipment continued to
decline at -1.2% pa in the US and -1% pa in the EU. Data for IT hardware show a similar
pattern. In contrast, data for national accounts intangibles show a stronger recovery in
investment following the financial crisis and the end of the ICT boom around 2000.18 Of
course, although nominal CT investment has been declining in recent years, that does not
mean that the real volume of CT investment has declined. That depends on the price per
unit of CT investment, which in turn depends partly upon the efficiency characteristic of
CT goods and how that has changed over time. In other words, £100 of telecoms investment
in 2013 has considerably greater real volume than £100 of investment in years previous.
Over the 1990s and early 2000s, investments in fibre optic cable and equipment increased
network capacity by a factor of forty (Doms, 2005). Doms (2005) also notes that the pace
of progress in fibre-optic capacity was well above that of Moore’s Law, with capacity
doubling every year between 1996 and 2001. Clearly an appropriate price index must take
this pace of technical change into account.

<hs>  Prices</hs>
  ~~~~~~

National price indices for value-added and GFCF are derived implicitly using current and
constant price data and re-referenced to 2005=1 with all volumes re-estimated.19 The key
lesson learned from research into the growth contribution of ICT equipment was the
required use of constant-quality deflators (see for example Triplett (2004)). Where
national practice is to not develop quality-adjusted deflators, researchers (or in some
cases, NSIs) have favoured the use of either: a) the US price index (which incorporates
some explicit quality adjustment) or some version adjusted for application to that
country; or b) sets of harmonised deflators across countries, such as those in EUKLEMS
(Timmer et al., 2007). Explicit quality adjustment (i.e hedonics) ensures that estimated
changes in price and volume reflect improvements in power and other characteristics, as
well as falls in listed prices, such that capital services better reflect changes in the
real quantity of capital available for production. Although hedonic adjustment is
sometimes regarded as superior, implicit quality adjustment methods (i.e matched models)
can yield similar estimates of price change to those uncovered using hedonic techniques,
provided the underlying data is sufficiently frequent and granular (Aizcorbe et al.,
2003).

     <hss>National practice in EU countries</hss>

        National practice in constructing CT investment price indices varies. Fig. 3
        presents national accounts CT GFCF deflators (blue) for each country in our
        datatset, compared with a harmonised CT deflator (red) from the OECD (Schreyer and
        Colecchia, 2002).20 From Fig. 3,21 national deflators for the US, Denmark,
        Portugal, Sweden, the UK and, to a lesser extent, Germany, show fast falling
        prices.22 In contrast, CT price indices for Austria, Spain, France, Ireland, Italy
        and the Netherlands are relatively flat with some exhibiting rising prices.
        National price indices for Belgium, Spain, Finland, France, Ireland, Italy and the
        Netherlands each have unusual features. That for Belgium exhibits price falls
        pre-2005, but price rises after. The index for Spain (ICT equipment index), shows
        rising prices until the 2000s, and gentle price falls for later years. Indices for
        Finland, Italy and the Netherlands are relatively flat pre-2005, but exhibit
        stronger price declines thereafter, and in the case of Finland, declines which are
        stronger than those in the harmonised index. The index for France is relatively
        flat throughout. Finally, that for Ireland is flat prior to 2005 before falling
        aggressively at a rate in line with the harmonised index, and then starting to
        rise such that it diverges strongly from the harmonised index. Since
        telecommunications equipment consists of tradeable goods, then under competitive
        conditions we would expect the law of one price to approximately hold, with some
        allowance for distribution margins, taxes and regulatory differences between
        countries. Therefore, as argued in Wyckoff (1995), we suggest that such divergence
        in measured prices reflects methodological differences between NSIs rather than
        real economic phenomena. Table 1 summarises our knowledge on the methods used to
        construct CT investment price indices in each country. We are currently unaware of
        any EU countries that apply hedonics in the estimation of CT investment prices.23
        Regarding the US index to which OECD estimates are harmonised, Colecchia and
        Schreyer (2002) report use of hedonics in the ’switching equipment’ component
        index. However, this actually refers to the incorporation of research prices
        indices (Grimm, 1996; 1997) in the historic series through to approximately 1998
        only.24 Thus, over the period for which we estimate, the US and therefore
        harmonised indices are not constructed from hedonic components.25 For most
        countries, including the US, matched model techniques are used instead, which as
        noted rely on detailed data in the cross-section and the time-series if they are
        to adequately account for fast quality change. In the US, the Federal Reserve
        Board price data, on which the Bureau of Economic Analysis (BEA) index is based,
        consist of weighted estimates from narrow product classes and are collected every
        quarter. Data for EU countries which also rely on matched model techniques exhibit
        far slower price falls, possibly because the data are not sufficiently detailed to
        observe fast improvements in quality.

        Harmonisation: Method and detail on underlying US index

        The red lines in Fig. 3 present the harmonised CT investment price index for each
        country, based on annual updates of the method described in Schreyer and Colecchia
        (2002). The method relies on the assumption that relative price changes for ICT
        assets move the same internationally as they do in the US. US ICT investment price
        indices are from the BEA. The BEA CT investment price index is a weighted
        aggregation of underlying indices, one of which is for “telephone switching
        equipment”, which previously (largely prior to the period considered in this
        study) incorporated hedonic adjustments (Colecchia and Schreyer, 2002) based on
        research from the Federal Reserve and others (Byrne and Corrado, 2015). Quality-
        adjustment since then in the official US data is implicit and based on matched
        model estimation.27

        National price indices vs harmonised indices: Advantages and disadvantages

        The most obvious criticism of harmonising prices across countries is that
        differences in recorded price change may reflect genuine differences in the
        (product) composition of GFCF between countries. Similarly, they may also reflect
        differences in industrial composition, market structure and/or the degree of
        competition. Consider software. Some proportion of software investment is own-
        account (in-house). Harmonisation of software prices with US prices (as in the
        OECD data) assumes that the composition of software investment across countries is
        similar to that in the US, which may be a strong assumption (Schreyer and
        Colecchia, 2002).28 and the argument that investors face the same price across
        countries is a more difficult one to make. For this reason we are more cautious in
        the interpretation of our results and the impact of harmonisation in the case of
        software. In response to these criticisms, we note however that first, as observed
        in Corrado (2011b), the pattern and profile of price changes in CT equipment is
        remarkably similar across a diverse range of technologies, products and varieties.
        Thus, an argument that differences such as those recorded in Table 1 are due to
        differences in the basket of goods does not appear credible, and the observation
        from Corrado suggests that harmonised indices provide a better approximation than
        an index which inadequately accounts for quality change. Second, CT capital
        equipment consists of tradeable goods. Therefore, with some allowance for margins,
        tariffs and other frictions, we would expect the law of one price to approximately
        hold in competitive conditions. Third, if the sources and methods of national
        statistical institutes (NSIs) fail to adequately account for quality change,
        estimates of capital input will be biased downward. Harmonising with an index
        which better accounts for quality change due to more detailed data, such as the US
        index, helps correct for that bias. It is also more appropriate than using a range
        of indices with different degrees of known inaccuracy. Fourth, price indices track
        changes rather than the price level itself. If the price of CT equipment changes
        at a similar rate across countries, but national price indices record changes at
        different rates, then harmonised indices will generate estimates of that are more
        accurate and consistent across countries. Further, if relative price (e.g. CT to
        non-ICT) changes are similar across countries, then the harmonisation method shown
        here can exploit this relation.29 Based on these advantages and the assumption of
        competitive pricing, the use of US ICT price indices has become accepted research
        practice, and in some cases they are also applied by NSIs in national
        measurement.30

<h>RESULTS</h>
-------

In this section we set out our growth-accounting results using alternative ICT investment
deflators.

<hs>  Sources of growth: EU-13 & US</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Fig. 4 compares a decomposition of US productivity growth with the EU-13, for periods
1996-00 and 2000-13, estimated using national accounts ICT investment deflators. Labour
productivity growth is higher in the US, in both periods, as is TFP growth and the
contribution of capital deepening. Within capital types, the contribution of CT capital
deepening is much less in the EU, as is the contribution of IT capital deepening and
intangible capital deepening, where the latter is dominated by software. This is confirmed
in Table 2 where we present a decomposition for the EU-13 compared to the US, first using
national accounts ICT deflators and second using harmonised ICT deflators. All estimates
are averages over 1996 to 2013. Column 1 is growth in value-added per hour worked (LPG);
column 2 is the contribution of labour composition (labour services per hour worked);
column 3 is the contribution of CT capital deepening (CT capital services per hour
worked); column 4 is the contribution of IT capital deepening; column 5 is contribution of
software capital deepening; column 6 is the contribution of capital deepening for all
other (non-ICT) assets; and column 7 is growth in TFP, estimated as column 1 minus the sum
of columns 2 to 6. The memo item in column 8 is the total ICT (IT, CT and software)
contribution and that in column 9 is the contribution of CT capital deepening as a share
of LPG, estimated as column 3 over column 1. Row 1 presents data for the US, row 2 for the
EU-13 using national accounts ICT deflators, and row 3 for the EU-13 using harmonised ICT
deflators. From column 1, we see that LPG was higher in the US, at 1.8% pa compared to
1.1% pa in the EU, whilst the contribution of labour composition was higher in the EU
(0.21% pa) than the US (0.17% pa). Column 3 presents the contribution of CT capital
deepening. Using national accounts deflators, the EU contribution was just over a quarter
of the US contribution, at 0.03% pa compared to 0.11% pa in the US. From the third row, we
see that applying harmonised ICT prices raises the EU CT contribution to 0.04% pa, but a
large disparity relative to the US remains. In the final row, we estimate that of the gap
relative to the US, over 1996 to 2013 just 15% of that gap can be explained by different
measures of price change. Column 9 presents the share of labour productivity growth
explained by CT capital deepening which is 6% in the US, compared to 2.5% in the EU using
national accounts deflators, and 3.6% in the EU using harmonised deflators. In column 4,
we estimate that the US contribution of IT hardware capital deepening stood at 0.19% pa
compared to 0.08% pa in the EU. Applying harmonised deflators raises the EU contribution
to 0.12% pa meaning that a larger proportion (25%) of the EU-US IT gap can be explained by
different measures of price change. In column 5 we present the contribution of software
capital deepening. Using national deflators that was 0.08% pa in the EU compared to 0.19%
pa in the US. Applying harmonised deflators raises the EU contribution to 0.13% pa so that
33% of the EU-US gap can be explained by different measures of price change. Column 8
conducts the same exercise for the contribution of total ICT capital deepening. Over
1996–2013, that was 0.47% pa in the US compared to 0.18% pa in the EU-13. Harmonisation of
ICT investment prices raises the EU contribution to 0.25% pa, meaning that of the gap
relative to the US, 28% can be explained by inconsistent estimates of price change. Thus,
for software, investment price harmonisation eliminates one-third of the gap relative to
the US, whilst for IT hardware and the ICT aggregate, one-quarter is eliminated. In
contrast, for CT equipment, only around one-sixth of the gap is eliminated.31
Harmonisation of ICT investment prices raises the contribution of ICT capital deepening in
the EU-13 and therefore lowers the contribution of TFP growth, which was just 0.15% pa in
the EU-13 compared to 0.55% pa in the US.

     <hss>Contribution of CT capital deepening</hss>

        Detailed growth-accounting results for each country, country group and asset are
        set out in Tables 6 and 7 in Appendix Balong with displays comparing growth
        contributions for each country relative to the US. To simplify, Fig. 5 presents
        estimates of the average contribution of CT capital deepening in each EU country
        relative to the US, using each alternative price index. The chart on the left is
        constructed using national accounts ICT deflators and the chart on the right using
        harmonised ICT deflators. Each country is presented relative to the US such that
        positive values represent growth higher than the US and negative values lower.
        Countries are ordered by country group: Scandinavia; Northern Europe (small);
        Northern Europe (large); and Southern Europe. For each country we present averages
        for two intervals: 1996-00 and 2000-13. Consider first the left-hand panel
        constructed using national accounts ICT deflators. The pattern is fairly uniform
        with contributions consistently smaller than the US, typically by around 0.1% pa.
        The exception is Sweden in the late 1990s, where CT capital deepening contributed
        0.24% pa of LPG compared to 0.16% pa in the US. In the 2000s the Swedish
        contribution weakened such that the CT contribution was less than the US, which
        also fell. Now consider the right-hand panel. With a few exceptions the pattern
        remains similar, with only a small reduction in the negative gap relative to the
        US for most countries. The countries for which applying harmonised deflators has
        the largest impact are Austria (in particular the second period), Portugal (in
        particular the first period), Ireland and Belgium.

     <hss>Contribution of IT capital deepening</hss>

        Below we present a similar comparison but this time for the contribution of IT
        (hardware) capital deepening. From the chart on the left, constructed using
        national accounts ICT deflators, there is a consistently large negative
        differential relative to the US for all countries in the late 1990s.32 The lower
        contribution of IT capital deepening in Europe relative to the US is a well-
        documented finding (see for example, van Ark et al. (2008)). Now moving to the
        chart on the right, constructed using harmonised ICT deflators, we see that the
        picture has changed considerably. The negative gap in relative IT contributions in
        the late 1990s is considerably smaller and for some countries is eliminated
        entirely. In the 2000s, the majority of countries move from having lower relative
        IT contributions to having comparable contributions that are in some cases higher
        than that in the US. Although there is some variation by country, we find that
        price harmonisation explains a much larger proportion of the gap relative to the
        US in the case of IT hardware than for CT equipment.

<hs>  Summary</hs>
  ~~~~~~~

Table 3 summarises some other key results. We present data for 2000-13 for broader country
groups on: the share of real CT investment in total real investment in 2000 and 2013
(columns 1 and 2); the share of nominal CT capital services in total nominal capital
services in 2000 and 2013 (columns 3 and 4); LPG (column 5); the contribution of CT
capital deepening (column 6); and the share of LPG accounted for by CT capital deepening
(column 7, estimated as column 6 over column 5). All results presented are estimated using
harmonised ICT deflators. From Table 3, columns 1 and 2, we see that real CT investment as
a share of total real investment was highest in the US, at 4.5% compared to 2.2% in the EU
in 2000, and at 5.3% compared to 3.1% in the EU in 2013. Data for EU country groups show
that the CT real investment share is fairly similar across the EU, in terms of these broad
regions. In 2000, it was highest in Scandinavia, and in 2013, it was highest in Southern
Europe. In the final row, we present data for Sweden and note that the CT investment share
in Sweden is higher than that for each EU country group and higher than the average for
all countries (first row) in both 2000 and 2013. As a share of real investment, over the
period CT investment has grown in all groups presented. The contribution of capital inputs
depends on the factor income share (elasticity) and growth in capital services. In columns
3 and 4 we present nominal CT capital services (i.e. CT user costs or CT factor income) as
a share of total nominal capital services (or gross operating surplus). First we note
that, unlike the real investment share, over the period the share of CT user costs in the
total has declined for all countries and country groups presented. Second, the CT income
share was higher in the US than the EU-13, at 4.7% compared to 2.5% in 2000, and at 2.9%
compared to 1.6% in 2013. CT income shares in EU country groups are strikingly similar to
those for the entire EU-13 but are higher in Sweden, where it is also higher than that of
the US in 2013. Columns 5, 6 and 7 present data on LPG, the contribution of CT capital
deepening and the share of growth accounted for by that contribution. Over the period, LPG
was strongest in the US, at 1.7% pa compared to 1% in the EU-13. Within the EU-13, LPG was
similar across country groups, at 1.1% pa, except for Southern Europe where it was weaker,
at 0.6% pa. Again, Sweden is an exception to this pattern with LPG of 1.5% pa, higher than
the all country average of 1.3% pa. On the contribution of CT capital deepening, column 6
shows that was highest in the US, at 0.09% pa compared to 0.04% pa in the EU-13. Within
the EU-13, the CT contribution was lowest in the large North European countries at 0.03%
pa and highest in Scandinavia at 0.05% pa. In the small North European and South European
economies it was the same as the EU-13 average at 0.04% pa. Again, the Swedish performance
stands out. There the CT contribution was higher than that in EU country groups, and the
all country average, and marginally lower than the US, at 0.08% pa. Column 7 presents the
share of LPG accounted for by the contribution of CT capital deepening. It is highest in
Southern Europe, at 7.1%, due to weak labour productivity growth of just 0.6% pa. In the
US, CT capital deepening explained 5.6% of LPG in the 2000s, compared to 3.9% in the
EU-13. EU country groups for which the share explained is higher than the EU-13 are
Southern Europe (7.1%) and Scandinavia (4.4%).

<h>CONCLUSIONS</h>
-----------

Numerous studies have documented technological advances in ICT and sought to measure its
contribution to growth. However the focus of those studies has generally been on the
contribution of total ICT equipment or total ICT including software. That focus on IT
hardware (or a group of assets dominated by IT hardware) means that the “C” in ICT has
received far less attention. In this paper, we carry out a sources of growth decomposition
for the US and thirteen EU countries and estimate the contribution of ICT capital under
different assumptions regarding its price, with a focus on the contribution of CT
equipment. We treat all three aspects of ICT capital including telecommunications
equipment (i.e. IT hardware, CT equipment and software) as distinct assets in the
estimation of capital services and test the impact of harmonising ICT investment prices
with those from the US. National price indices for each ICT asset vary considerably but
for all time periods we find that the contribution of CT capital deepening is positive for
all countries and country groups and lies in the range of 0 to 0.24% pa. In general, the
CT contribution was highest in the late 1990s and has declined in the 2000s. For the
period 1996–2013, the contribution of US CT capital deepening is estimated at 0.11% pa in
the US compared to 0.03% in the EU when using official national accounts investment price
indices. Re-estimating capital services using harmonised ICT deflators raises the EU CT
contribution to 0.04% pa, but a large disparity relative to the US remains. We estimate
that of the gap relative to the US over 1996 to 2013, just 15% can be explained by
different estimates of price change. In comparison, using national accounts prices, the US
contribution of IT hardware stood at 0.17% pa against 0.07% pa in the EU. Applying
harmonised prices raises the EU contribution to 0.09% pa meaning that one-quarter of the
EU-US gap can be explained by different measures of price change. For software, using
national accounts indices the US and EU growth contributions are 0.19% pa and 0.08% pa
respectively. Price harmonisation raises the EU contribution to 0.12% pa meaning that a
third of the gap in contributions can be explained by differing estimates of price change.
Thus, for all forms of ICT capital, we estimate growth contributions in the EU that are
considerably lower than those estimated for the US. However, only a small proportion of
that gap is eliminated once we harmonise ICT investment prices with US official estimates.
Of all ICT assets, that proportion eliminated is smallest in the case of CT capital.
Within the EU and over the period 2000-13, growth in real CT investment is strongest in
Sweden. As a share of real investment, CT investment is higher in Sweden than the US, as
is the CT factor income share which partly depends on the rate of past investment.
Similarly, the CT contribution in Sweden was higher than that for all EU country groups
and marginally lower than that for the US, at 0.08% pa. In summary, there are still
considerable disparities in measures of ICT investment price change across OECD countries.
However, these disparities do not explain lower ICT growth contributions in the EU
relative to the US. This is particularly so for CT capital, where inconsistencies in
estimates of price change only explain approximately 15% of the EU-US gap. The remaining
disparity in the contribution is therefore due to a lower rate of CT investment in the
EU-13, in the sense of both current and past investments, which determine growth in
capital services and the level of the real stock.33 Thus variation between countries is
likely affected by issues such as public policy, public finances and public investment in
cases where some part or all of the network infrastructure remains in the non-market
sector. The timing of network build-out and adoption lags are also likely a cause of
variation between countries.


<h>REFERENCES</h>
----------

  [2] Bart Van Ark, Mary O'Mahony, Marcel P. Timmer. The productivity gap between Europe and the United States: Trends and causes. doi:10.1257/jep.22.1.25
  [7] Alessandra Colecchia, Paul Schreyer. ICT investment and economic growth in the 1990s: Is the United States a unique case?. doi:10.1006/redy.2002.0170
  [14] Jukka Jalava, Matti Pohjola. The roles of electricity and ICT in economic growth: Case Finland. doi:10.1016/j.eeh.2007.11.001
  [15] Dale W. Jorgenson, Kevin J. Stiroh. Raising the speed limit: U.S. Economic growth in the information age
  [17] Dale W. Jorgenson. Information technology and the U.S. Economy. doi:10.1257/aer.91.1.1
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<ART>The impacts of workers' remittances on human capital and labor supply in developing countries
================================================================================

Authors: Seyed Soroosh Azizi
DOI: 10.1016/j.econmod.2018.07.011
Year: 2018  |  Pages: 377-396
ASJC codes: 2002
Keywords: Developing countries, Education, Health, Human capital, Labor supply, Migration, Remittances

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

This study investigates the impacts of workers' remittances on human capital and labor supply by using data for 122 developing countries from 1990 to 2015. This topic has not been explored thoroughly at the aggregate level, mainly due to endogeneity of remittances and the difficulty in finding instruments to resolve this issue. To address the endogeneity of remittances, I estimate bilateral remittances and use them to create weighted indicators of remittance-sending countries. These weighted indicators are used as instruments for remittance inflow to remittance-receiving countries. Results obtained in this study indicate that remittances raise per capita health expenditures and reduce undernourishment prevalence, depth of food deficit, prevalence of stunting, and child mortality rate. Remittances also raise school enrollment, school completion rate, and private school enrollment. Although there is no difference in the impact of remittances on the health outcome of boys and girls, remittances improve the educational outcome of girls more than the educational outcome of boys. Further, remittances decrease the female labor force participation rate but do not affect the male labor force participation rate.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Between 1990 and 2015, the number of individuals living outside their countries of birth
grew from 153 million people to 244 million people, which corresponds to 2.87% of the
world population in the year 1990 and 3.32% of the world population in the year 2015
(United Nations). The total amount of remittances received has risen from $68 billion in
1990 to $553 billion in 2015. The average amount of money each migrant remitted (in 2011
constant dollars) has risen from $688 in 1990 to $2128 in 2015. These amounts include only
remittances that have been sent through official channels (the World Bank, United Nations,
author's calculations). This surge in the value of remittances has attracted the attention
of many researchers. During recent years, different aspects of remittances have been under
the scrutiny of researchers. One of the main aspects of remittances is impacts of
remittances on remittance-receiving countries. The inflow of remittances can affect
remittance-receiving countries in a variety of subjects such as the growth impact of
remittance (Rao and Hassan, 2011; Gapen et al., 2009; Giuliano and Ruiz-Arranz, 2009;
Ziesemer, 2012); the impact of remittances on poverty and inequality (Acosta, 2006; Adams
and Page, 2005; Li and Zhou, 2013; Bang et al., 2016); remittances and financial
development (Brown et al., 2013; Aggarwal et al., 2011; Coulibaly, 2015; Chowdhury, 2011);
environmental effects of remittances (Li and Zhou, 2015); the impact of remittances on
labor productivity (Al Mamun et al., 2015); the impact of remittances on political
institutions (Williams, 2017). Although most researchers have investigated the impacts of
remittance inflows on remittance-receiving countries, there are few studies on the impacts
of remittance outflows on remittance-sending countries (Hathroubi and Aloui, 2016;
Alkhathlan, 2013). There is a clear distinction between the remittance inflow to
developing countries and the remittance inflow to developed countries. In the year 2015,
the average workers' remittances to GDP ratio for developing country was 2% and for
developed countries was 0.6%. Remittance to developed countries is not the primary
interest of this paper; instead, the impacts of remittances on human capital and labor
supply in developing countries is explored in this paper. In the past few years, many
researchers have examined the impact of remittances on human capital or labor supply in a
specific country or region. The primary barrier in evaluating the impact of remittances on
human capital, in case of all developing countries, is endogeneity of remittances.
Remittances are endogenous to education, health outcomes, and labor supply of those left
behind. Reverse causality, common factors affecting both remittances and human capital,
and measurement error are among the sources of endogeneity. Finding instruments to
overcome endogeneity of remittances in one country is easier than finding valid and strong
instruments for remittances in all developing countries. To address the endogeneity of
remittances, this research uses a novel instrumental variable (IV) approach by
incorporating three economic indicators of the remittance-sending countries as
instruments: per capita Gross National Income (GNI), unemployment rate, and real interest
rate. Since each remittance-receiving country has many countries as the sources of
remittances, building the instruments requires knowing the bilateral remittances to
calculate the weighted average indicators of the remittance-sending countries. Because
bilateral remittances are not generally available, I estimate them and use them as weights
to build the instruments. This estimation strategy allows me to utilize three valid and
strong instruments, which are related to remittance-sending countries, to investigate the
impacts of workers' remittances on human capital and labor supply in remittance-receiving
countries. I also use this IV approach to study gender-specific impacts of remittances on
health, education, and labor supply in developing countries. The results obtained in this
paper indicate that remittances raise per capita out-of-pocket health expenditures and per
capita total health expenditures and reduce undernourishment prevalence, depth of food
deficit, prevalence of stunting, and child mortality rate. Remittances also raise school
enrollment, school completion rate, and private school enrollment. As a robustness check,
this paper investigates the overall impact of remittances on Human Development Index (HDI)
and shows that remittances increase HDI. Another contribution of this paper is showing the
gender-specific effects of remittances. Although there is no difference in the impact of
remittances on the health outcome of boys and girls, remittances raise the education
investment in girls more than in boys. Further, remittances decrease the female labor
force participation rate but do not affect the male labor force participation rate.
Remittances can lift budget constraints, thereby providing children in remittance-
receiving households the opportunity to go to school or have better health outcomes. While
remittances can benefit households by lifting liquidity constraints, migration of a family
member can have a negative impact on the household's well-being. Migration of a productive
family member may have disruptive effects on the life of the household. These observations
lead to a fundamental development question: do remittances to developing countries
contribute to higher investment in human capital? This research examines this question by
exploring the major factors influencing education and health outcomes in developing
countries. This paper addresses three main questions: To what extent can the remittances
to developing countries improve health and education outcomes in terms of nutrition
adequacy, mortality rates, school attendance, and educational attainment? If the
remittances can influence the children's health outcome, school attendance, and
educational attainment, is there any difference between the genders? What is the impact of
remittances on labor force participation for men and women? As major components of human
capital, health and education impact long-run economic growth. Therefore, answering these
questions is crucial to evaluate the overall effect of workers' remittances on developing
countries. The rest of the paper is arranged as follows. Background and literature review
is provided in section 2. Section 3 discusses the data used in this paper. Section 4 is
devoted to the econometric model. Section 5 presents empirical results, and Section 6 some
conclusions.

<h>BACKGROUND</h>
----------

Early studies on impacts of remittances on human capital (both health and education),
financial development, poverty and inequality, and exchange rates did not consider the
endogeneity of remittances. However, most of the recent studies about the impact of
remittances on different aspects of remittance-receiving households and countries
recognize the endogeneity of remittances and include different methodologies to resolve
the problem of endogeneity of remittances. The traditional and most popular method of
addressing the endogeneity of remittances is to use instrumental variables. While the
instruments must be strong, the bigger challenge to researchers is to find valid (i.e. not
correlated with the error term) instruments. Generally, three categories of instruments
are used by different authors: instruments related to remittance-receiving countries,
instruments related to remittance-sending countries, and instruments related to the cost
of remittances. Not many papers have addressed the endogeneity of remittances at the
aggregate level. Adams and Page (2005) is one of the first studies which addresses
endogeneity of remittances in the country-level. They use three instrumental variables to
account for endogeneity of the impact of remittances on poverty. The first instrument is
the distance (miles) between the four major remittance-sending areas and remittance-
receiving countries. The second instrument used by them is the percentage of the
population over age 25 that has completed secondary education. This variable is correlated
with education, and it is not a valid instrument in this research. The third variable used
by them is government stability. The effect of government stability on remittances can be
positive (if migrants have investment incentives, they remit more if their home countries
are more stable) or negative (if migrants have altruistic incentives, they remit more if
their home countries are less stable). Government stability also can be correlated with
educational attainment and health outcome. This section is divided into three parts.
First, a summary of papers which study the effects of remittances on health outcomes is
provided. Then, papers which investigate the impacts of remittances on education are
reviewed. Lastly, papers which examine the impacts of remittances on labor supply are
summarized. Due to the importance of the endogeneity issue, special attention is paid to
the instruments used by different authors.

<hs>  Remittances and health</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

Researchers who have studied the impact of remittances on health outcome mainly focused on
three health measurements: health expenditures, nutrition status, and child mortality
rates. In the following, I briefly discuss papers who consider the impacts of remittances
on these three aspects of health outcome. Note that health expenditure is not an aspect of
health outcome per se, but it has a strong impact on health outcome. Ambrosius and
Cuecuecha (2013) test the assumption that remittances are a substitute for credit by
comparing the response to health-related shocks using Mexican household panel data. They
find that the occurrence of serious health shocks that required hospital treatment doubled
the average debt burden of households with a member having a health shock compared to the
control group. However, households with a parent, child, or spouse in the US did not
increase their debts due to health shocks. The authors use weighted linear regression to
address the endogeneity problem. Therefore, in the case of Mexican families with a member
facing a health shock, it can be concluded that remittances can play a substitute role for
credit. Valero-Gil (2009) considers the effect of remittances on the share of health
expenditures in total household expenditure in Mexico and finds a positive and
statistically significant effect of remittances on the household health expenditure
shares. The paper concludes that health expenditure is a target of remittances, and a
dollar from remittances is being devoted in part to health expenditures. The author uses
the percentage of return migration between 1995 and 2000 at the municipal level as an
instrument for remittance. Amuedo-Dorantes and Pozo (2011) find that international
remittances raise health care expenditures among remittance-receiving households in
Mexico. They select two variables to be included as instruments: the road distance to the
US border (from the capital of the Mexican state in which the household resides) and US
wages in Mexican emigrant destination states. Their results suggest that 6 Pesos of every
100 Peso increment in remittance income are spent on health. Ponce et al. (2011) study the
impact of remittances on health outcomes in Ecuador, and they do not find significant
impacts on long-term child health variables. However, they find that remittances have an
impact on health expenditures. They use historic state-level migration rates as an
instrument for current migration shocks. Some researchers have used a variety of
measurements of nutrition status as the factor representing health outcome. Food security
level, household food consumption, child nutritional status, and low birth weight are some
of the measurements of nutrition status. In the following, I introduce four of these
papers. Generoso (2015) analyzes the main determinants of household food security using a
survey conducted in Mali in 2005. The author uses a partial proportional odds logit model
and shows that the diversification of income sources, through the reception of
remittances, constitutes one of the main ways of coping with the negative impact of
climate hazards on food security. Combes et al. (2014) explore the role of remittances and
foreign aid inflows during food price shocks. They conclude remittance and aid inflows
dampen the effect of the positive food price shock and food price instability on household
consumption in vulnerable countries. Anton (2010) analyzes the impact of remittances on
the nutritional status of children under five years old in Ecuador in 2006. Using an
instrumental variables strategy, the study finds a positive and significant effect of
remittance income on short-term and middle-term child nutritional status. The author uses
the number of Western Union offices per 100,000 people at the province level as the
instrument. Frank and Hummer (2002) find that membership in a migrant household provides
protection from the risk of low birth weight among Mexican-born infants largely through
the receipt of remittances. They did not account for endogeneity of remittances. Many
researchers have used child and infant mortality rates as the factor representing health
outcome. Reducing child mortality rate is one of the United Nations Sustainable
Development Goals (SDG). The goal is by 2030 to end preventable deaths of newborns and
children under five years of age, with all countries aiming to reduce neonatal mortality
to less than 12 per 1000 live births and under-5 mortality to less than 25 per 1000 live
births. In the following, some of these studies are discussed. Terrelonge (2014) examines
how remittances and government health spending improve child mortality in developing
countries and concludes remittances reduce mortality through improved living standards
from the relaxation of households' budget constraints. Chauvet et al. (2013) consider the
respective impact of aid, remittances and medical brain drain on the child mortality rate.
Their results show that remittances reduce child mortality while medical brain drain
increases it. Health aid also significantly reduces child mortality, but its impact is
less robust than the impact of remittances. Kanaiaupuni and Donato (1999) consider the
effects of village migration and remittances on health outcomes in Mexico and conclude
higher rates of infant mortality in communities experiencing intense U.S. migration. On
the other hand, mortality risks are low when remittances are high. Zhunio et al. (2012)
study the effect of international remittances on aggregate educational and health outcomes
using a sample of 69 low- and middle-income countries. They find that remittances play an
important role in improving primary and secondary school attainment, increasing life
expectancy and reducing infant mortality.

<hs>  Remittances and education</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~

To investigate the impact of remittances on the education of those left behind, most of
the researchers rely on school attendance as the main indicator of education. Many authors
also examine the impact of remittances on child labor. The common belief is that if
remittances decrease child labor, then they increase children's education. While school
attendance frequently is used to measure investment on education, it represents the
quantity of education and fails to capture the quality of education. Therefore, some
researchers have used private school enrollment to demonstrate the quality of education.
There are two theories about the impact of migration and remittances on education. On the
one hand, as Bouoiyour and Miftah (2016) state, parents invest in the education of their
children if they believe such investment generates a higher rate of return than the return
on savings. Some parents in low-income households invest too little in the education of
their children because they cannot afford to finance educational investments regardless of
such returns. Hence, it is expected that the reduction of these liquidity constraints will
make education more accessible to children from poor families. Therefore, financial
transfers from family members can lift the budget constraints and allow parents to invest
in the education of their children to the extent that is optimal for them. On the other
hand, as Amuedo-Dorantes and Pozo (2010) state, the presence of family members abroad may
induce changes in school attendance of children in migrants' households for a variety of
reasons. Children may have less time to devote to schooling because they engage in market
activities to earn income to defray migration-related expenses of households.
Alternatively, children may leave school to perform necessary household chores that the
absent migrant no longer attends to. Finally, if children get encouraged to migrate in the
future, they may drop out of school if the origin country's education is not generally
well-recognized in the destination. Among researchers who consider the impact of
remittances on education and address the endogeneity of remittances, two instruments are
used frequently. Some studies that recognize the endogeneity of migration and remittances
use migration networks as the instrument. Many studies have used economic indicators of
remittance-sender countries as instruments for remittances. The following papers have used
migration networks as the instrument for remittances. Bouoiyour and Miftah (2016) use the
history of migration networks and remittances costs as instruments to address the
endogeneity of remittances. They find that the receipt of remittances in rural areas of
southern Morocco has a significant positive effect on school attendance, especially for
boys. Acharya and Leon-Gonzalez (2014) explore the effects of migration and remittance on
the educational attainment of Nepalese children. Their results indicate that remittances
help severely credit-constrained households enroll their children in school and prevent
dropouts. Also, remittances help households that face less severe liquidity constraints
increase their investment in the quality of education. By using migration networks as
instruments, the authors gain similar results. Acosta (2011) studies the effects of
remittance receipt on child school attendance and child labor in El Salvador. The paper
uses El Salvadorian municipal-level migrant networks and the number of international
migrants who returned two or more years ago as instruments to address the endogeneity of
remittances. The author concludes insignificant overall impact of remittances on
schooling; a strong reduction of child wage labor in remittance recipient households; and
an increase in unpaid family work activities for children in those households. Moreover,
while girls seem to increase school attendance after remittance receipts by reducing labor
activities, boys, on average, do not benefit from higher education. Alcaraz et al. (2012)
study the effects of remittances from the U.S. on child labor and school attendance in
recipient Mexican households. They use distance to the U.S. border along the 1920 rail
network as an instrument for the membership in the remittance recipient group. By using
the differences-in-differences method, they find that the negative shock on remittance
receipts in 2008–2009 caused a significant increase in child labor and a significant
reduction of school attendance. As stated by Salas (2014) the common belief is that
private schools provide better education compared to that provided by public schools.
Besides increasing school enrollment, remittances can affect the choice of school type.
The main limitation to access private education in developing countries is its cost.
Remittances can lift the budget constraints and allow parents to invest in the quality of
education of their children, as well as its quantity. Salas investigates the effect of
international migration on children left behind in Peru. Historical department-level
migration rate is used as an instrument for remittances. The model analyzes the role of
international remittances on the investment decision between sending children to a public
school or to a private school and finds that international remittances have a positive
effect on the likelihood to send children to private schools. While using migration
networks to address the endogeneity of migration allows us to assess the impact of
migration on educational attainment, it is not the best possible instrument if we are
interested in impacts of remittances on educational attainment. Using economic indicators
of remittance-sending countries is more useful if we want to evaluate the impacts of
remittances on investment in education. The following studies use economic indicators of
remittance-sending countries to address the endogeneity of remittances. Calero et al.
(2009) investigate how remittances affect human capital investments through relaxing
resource constraints. They use information on source countries of remittances and regional
variation in the availability of bank offices that function as formal channels for
receiving remittances. They show that remittances increase school enrollment and decrease
the incidence of child work, especially for girls and in rural areas. Besides increasing
school enrollment, remittances affect the choice of school type. Remittances lead to a net
substitution from the public to private schooling, hence increasing the quality of human
capital investments in children. Bargain and Boutin (2015) explore the effects of
remittance receipt on child labor in Burkina Faso. They use economic conditions in
remittance-sending countries as instruments for remittances. The authors conclude while
remittances have no significant effect on child labor on average, they reduce child labor
in long-term migrant households, for whom the disruptive effect of migration is no longer
felt. Fajnzylber and Lopez (2008) argue that in 11 Latin American countries with the
exception of Mexico, children of remittances-receiving families are more likely to remain
in school. The positive effect of remittances on education tends to be larger when parents
are less educated. The authors use two external instruments based on the real output per
capita of the countries where remittances originate. Amuedo-Dorantes et al. (2010) address
the endogeneity of remittance receipt and find that the receipt of remittances by the
households in Haiti lifts budget constraints and raises the children's likelihood of being
schooled, and the disruptive effect of household out-migration imposes an economic burden
on the remaining household members and reduces children's school attendance. They use two
variables as instruments: weekly earnings of workers in the United States who are similar
to potential Haitian remitters, and unemployment in those geographic areas in which the
household is likely to have migrant networks. Some other papers use other instrumental
variables or do not address the endogeneity of remittance. Bansak and Chezum (2009)
examine the impact of remittances on educational attainment of school-age children in
Nepal, focusing on differences between girls and boys. They use past literacy rates and
political unrest by the district as instrumental variables to address the endogeneity.
Their results indicate that positive net remittances increase the probability of young
children attending schools. Yang (2008) concludes that favorable shocks in the migrants'
exchange rates (appreciation of the host counties' currency versus Philippine peso) lead
to enhanced human capital accumulation in origin households, a rise in child schooling and
educational expenditure, and a fall in child labor. Edwards and Ureta (2003) examine the
effect of remittances from abroad on households' schooling decisions using data for El
Salvador. They examine the determinants of school attendance and find that remittances
have a large and significant effect on school retention. The main issue with their paper
is that they do not recognize the problem of endogeneity. Acosta et al. (2007) explore the
impact of remittances on poverty, education, and health in eleven Latin American
countries. While remittances tend to have positive effects on education for all Latin
American countries with the exception of Jamaica and the Dominican Republic, the impact is
often restricted to specific groups of the population (e.g. the positive effect of
remittances on education tends to be larger when parents are less educated).

<hs>  Remittances and labor supply</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Researchers who study the impact of remittances on labor supply in remittance-receiving
countries mainly focus on two aspects of labor supply: labor force participation rate and
hours worked per week. As argued by Cox-Edwards and Rodriguez-Oreggia (2009), an important
concept underlying the labor force participation decision is the notion of the reservation
wage. The reservation wage is the lowest wage rate at which a worker would be willing to
accept a particular type of job. A job offer involving the same type of work and the same
working conditions, but at a lower wage rate, would be rejected by the worker. An increase
in the reservation wage would reduce the probability that an individual participates in
the labor force. One of the determinants of the reservation wage is non-labor income,
which for an individual is a function of his or her own assets and the amount of income of
other household members. The higher the level of income of the rest of the household (e.g.
remittances), the higher the reservation wage of the individual, and the lower the
probability that he or she participates in the labor force. Many researchers have looked
at remittances as an additional non-labor income for recipient households and hypothesized
that the presence of remittances would lead to a reduction in labor force participation
among recipient household members. In studying the impact of migration and remittances on
labor supply in recipient-households and receiving-countries, migration and remittances
are endogenous. Migration and remittances are correlated with the error term due to a
variety of factors. Reverse causality, omitted variable bias (uncontrolled common factors
affecting both migration and remittances and labor supply) and measurement errors are
among the potential sources of endogeneity. If the migrant's decision on how much to remit
depends on whether the family members are looking for a job or not, reverse causality
exists. Omitted variable bias may exist if remittances are related to the remittance-
recipient family members' wealth or ambition, which may be correlated to the labor supply
by the recipient. Many researchers use instrumental variables to address the endogeneity
of migration and remittances. Particularly, migration networks are used frequently to
address the endogeneity of migration and remittances. In the following, I review some
papers which used this approach. Nguyen and Purnamasari (2011) apply an instrumental
variable estimation method, using historical migration networks as instruments for
migration and remittance receipts and find that, in Indonesia, migration reduces the
working hours of remaining household members. Hanson (2007), based on rural households in
Mexico in 2000, concludes individuals are less likely to participate in the labor force if
their household either has sent migrants abroad or received remittances from abroad. The
author also finds that women from high-migration states become less likely to work
relative to women from low-migration states. The author argues that the unobserved
characteristics of households that affect labor supply are also likely to affect whether
households choose to send migrants abroad, and uses historical emigration rates as one of
the approaches to address the endogeneity issue. Acosta (2006) controls for household
wealth and uses selection correction techniques and concludes that, in El Salvador,
remittances are negatively related to the adult female labor supply. However, on average
adult male labor force participation remains unaffected. The author recognizes the
endogeneity issue and uses the village migrant networks and the number of international
migrants who returned two or more years ago as instruments for remittance receipts. Many
authors use other instruments to address the endogeneity of remittances. For example,
Amuedo-Dorantes and Pozo (2006) assess the impact of remittances on Mexicans labor supply.
They use per capita count of Western Union offices in the state as an instrument for
addressing the endogeneity of remittances. They conclude while overall male labor supply
does not vary because of changes in remittance income, its composition by type of
employment does. Unlike men, the overall female labor supply decrease due to changes in
remittance income, although only in rural areas. Acosta et al. (2008) conclude that in all
10 Latin American and Caribbean countries examined, remittances have a reducing effect on
the number of hours worked per week. This negative effect is present both in urban and
rural areas. Afterward, remittances are instrumented with the share of remittance-
receiving households in the country interacted with household characteristics that affect
their likelihood to migrate. After instrumenting for endogeneity, their negative impact on
labor force participation ceases to be significant in a number of cases. They also find
that the reductions in labor supply caused by remittances tend to be much smaller among
individuals with higher levels of schooling. Some researchers use other methods to address
the endogeneity of remittances, or they do not address this problem at all. Guha (2013)
states that with an increase in the non-wage income, such as remittances, the households
will work less and have more leisure, as the loss in the wage income gets compensated by
the remittance income. The author uses international remittances to Bangladesh as the
reference case, and applies Dynamic Stochastic General Equilibrium (DSGE) model, to show
that a sudden increase in foreign remittances results in a fall in the labor supply to the
traded sector and a decline in the output in the traded sector. Cox-Edwards and Rodriguez-
Oreggia (2009) use propensity score matching to separate persistent from sporadic
remittances. They find limited evidence of labor force participation effects of persistent
remittances. This implies that remittances are an integral part of remittance recipient
households' income generation strategy. Acosta et al. (2009) find that in El Salvador an
increase in remittance flows leads to a decline in labor supply. Kim (2007) studies the
reasons for the coexistence of high unemployment rates with increasing real wages in
Jamaica. The author concludes that households with remittance income have higher
reservation wages and reduce labor supply by moving out of the labor force. Funkhouser
(2006) uses longitudinal data from 1998 and 2001 in Nicaragua to examine the impact of the
emigration of household members on household labor market integration and poverty. The
author concludes that households with emigrant had a reduction in labor income compared to
otherwise similar households.

<h>DATA</h>
----

This study examines 122 developing (poor and middle-income) countries1 from the six major
developing world regions: Latin America and the Caribbean, sub-Saharan Africa, the Middle
East and North Africa, East Asia and the Pacific, South Asia, and Europe and Central Asia.
The income and regional classification in this paper follow the conventions of the World
Bank. This panel of countries is sufficiently diverse, which means that these results are
internationally applicable. The annual data has a time span of 1990–2015. All dollar
values in this paper are constant 2011 US dollars. Data on remittances come from the
International Monetary Fund (IMF), which has defined remittances as the sum of two
components: personal transfers (workers' remittances) and compensation of employees. The
World Bank has adopted the same definition. Compensation of employees refers to the income
of border, seasonal, and other short-term workers who are employed in an economy where
they are not resident and of residents employed by nonresident entities. Being present for
one year or more in a territory or intending to do so is sufficient to qualify one as
being a resident of that economy (IMF, 2009). Between 1990 and 2015, personal transfers
constituted 66% of remittances, and compensation of employees constituted 34% of
remittances. In the year 2015, these ratios were 65% and 35% respectively. As Chami et al.
(2009a) and Chami et al. (2009b) show, this aggregation is not appropriate since the two
different types of transfers have different properties and respond differently to economic
shocks. Thus, I follow Combes et al. (2014) in using only workers' remittances as the
measure of remittances. Therefore, the narrow definition of remittances (workers'
remittances) is used in this paper to record remittances. Remittances are divided by
remittance-receiving countries' populations and converted in constant 2011 international
dollars. The income variable in equation (1) is per capita Gross Domestic Product (GDP) in
constant 2011 international dollars adjusted for purchasing power parity (PPP). In this
paper, I report the impacts of remittances on two types of human capital: health outcomes
and educational attainment. After investigating the impacts of remittances on health
outcomes and educational attainment, as a robustness check, I examine the effect of
remittances on HDI. Finally, I estimate the impact of workers' remittances on labor force
participation. To fully investigate the impacts of workers' remittances on all aspects of
health and education outcomes in developing countries, nine health measurements and nine
education indicators have been used as dependent variables. Using different health and
education measurements is an excellent robustness check and ensures that demonstrated
positive impacts of remittances on health and education outcomes do not happen by chance.
Nine health measurements are examined in this research: per capita out-of-pocket health
expenditure, per capita total health expenditure, life expectancy at birth,
undernourishment prevalence, depth of food deficit, prevalence of stunting, neonatal
mortality rate, infant mortality rate, and under-five mortality rate. Although per capita
out-of-pocket health expenditure and per capita total health expenditure are not measures
of health, because they have direct effects on health outcomes, they are included as two
of the health outcome measurements. Seven explanatory variables are employed in health
regressions as the covariates: per capita GDP, population over 65, urban population share,
health expenditure to GDP ratio, food production index, government expenditure on
education, and newborns protected against tetanus. Nine educational measurements are
chosen in this paper: pre-primary gross enrollment rate, primary gross enrollment rate,
secondary gross enrollment rate, tertiary gross enrollment rate, percent of children out
of primary school, private primary enrollment rate, secondary compliment rate, primary
compliment rate, and gender parity index for primary education. Two new explanatory
variables are employed in the education section: Labor force participation and government
expenditures on education as a percentage of GDP. Table 1 describes all dependent and
explanatory variables alongside their descriptive statistics. Table 2 provides descriptive
statistics for gender-specific variables. Except for remittances and HDI, data on all
dependent and explanatory variables are from the World Development Indicators. HDI data
are from the United Nations Development Programme (UNDP). This study uses three
instruments to address the endogeneity of workers' remittances: weighted average per
capita GNI, unemployment rate, and real interest rate of remittance-sending countries.
Data on GNI and populations are from the United Nations. Data on unemployment rates and
real interest rates are from the World Development Indicators. The real interest rate is
defined as lending interest rate adjusted for inflation as measured by the GDP deflator.
Data on out-of-pocket health expenditures and total health expenditures cover the years
between 1995 and 2014. The share of out-of-pocket health expenditures in total health
expenditure in developing countries has fluctuated in recent years. In 1995 and 2014 it
was 40.8% and 36.2% respectively. However, there has been a stable increasing trend in the
amount of per capita total health expenditure and per capita out-of-pocket health
expenditure: they went up from $131.4 and $53.6 in the year 1995 (expressed in constant
2011 US dollars adjusted for PPP) to $530.3 and $191.9 in the year 2014 respectively. In
recent years there has been a remarkable decline in undernourishment prevalence, depth of
food deficit, and child mortality rates across the developing world. Undernourishment
prevalence data cover years 1991–2015. Average undernourishment prevalence went down from
23.7% in the year 1991 to 12.67% in the year 2015. Depth of food deficit data cover years
1992–2015. Average depth of food deficit decreased from 175.6 kilocalories in the year
1992 to 91.9 kilocalories in the year 2015. In 1990, average neonatal, infant, and under-
five mortality rates per 1000 live births were 39.3, 69.1, 99.7 respectively. In 2015,
average neonatal, infant, and under-five mortality rates declined to 20.8, 34.6, and 46.4
respectively, in the developing world. As UNDP states, HDI is a summary measure of average
achievement in key dimensions of human development: a long and healthy life, being
knowledgeable, and having a decent standard of living. The HDI is the geometric mean of
normalized indices for each of the three dimensions. The health dimension is assessed by
life expectancy at birth, the education dimension is measured by the mean of years of
schooling for adults aged 25 years and more, and expected years of schooling for children
of school age. The standard of living dimension is measured by gross national income per
capita. The HDI uses the logarithm of income, to reflect the diminishing importance of
income with increasing GNI. The scores for the three HDI dimension indices are then
aggregated into a composite index using geometric mean. Data on HDI are adopted from UNDP.
While HDI data cover the years 1990–2015, male and female HDI data cover the years 2000,
2005, and 2010 to 2015. In recent years there has been a slight but smooth and stable
decreasing trend in labor force participation rates in developing countries. In 1990,
total, male, and female average labor force participation rates in developing countries
were 68.1%, 82.7%, and 53.4% respectively. In 2015, total, male, and female average labor
force participation rates in developing countries were 63.5%, 77.9%, and 48.9%
respectively.

<h>ECONOMETRIC MODEL</h>
-----------------

for i = 1, …, N and t = 1, …, Ti where H is a measure of health, education, HDI, or labor
supply in country i at time t, β0 is the intercept, Rit is the per capita remittances
received by country i at year t, Iit is the mean per capita income of country i at year t,
Xit is a vector of other variables that potentially affect Hit, δi is region dummy and eit
is the error term. Since all variables are in logarithm, β1 can be interpreted as the
elasticity of human capital with respect to per capita remittances and β2 can be
interpreted as the elasticity of human capital with respect to per capita income. The
reason that region dummies are used in this research rather than country dummies is that
for many countries, there is just one year of data available, and for using country-
specific effects, those countries had to be dropped from the regression. To avoid dropping
those countries, I used region-specific fixed effects rather than country-specific fixed
effects. All six major developing world regions are included: Latin America and the
Caribbean, sub-Saharan Africa, the Middle East and North Africa, East Asia and the
Pacific, South Asia, and Europe and Central Asia. The income and regional classification
in this paper follow the conventions of the World Bank. I followed Adams and Page (2005)
in using region-specific effects as fixed effects. However, in those cases that more than
one year of data were available for each country, as a robustness check, I also estimated
the regressions by using country-specific effects. The results were similar in terms of
sign and significance of the parameter estimates but magnitudes were slightly different.
Correlation matrix between selected variables is provided in Appendix I. Several
correlation coefficients are high, therefore, in order to avoid multicollinearity effect
arising from that, as a general rule, I try to not include highly correlated explanatory
variables in a same regression equation. For example, in regressions corresponding to the
impact of remittances on child mortality rate, rather than the dollar value of health
expenditures, the ratio of health expenditures to GDP is used. Also, in all regression
equations for the case of the impact of remittances on education, rather than the dollar
value of government expenditure on education, its ratio to GDP is used.2 Some of the
variables used in the regression models, like per capita GDP, are non-stationary in the
level, but they are first-difference stationary. Since there are non-stationary variables
in the regression models, the results of the regressions might be spurious. To check
whether the results of the regressions are spurious or not, for the regressions with non-
stationary dependent variables, I implement panel cointegration tests. If cointegrations
exist, then it can be concluded that the error term is stationary, which means the results
of the regressions are not spurious. Two tests are used to check whether panel
cointegrations exist: the Kao Residual Cointegration Test proposed by Kao (1999) (also
known as the residual-based Augmented Dicky Fuller test) and the Johansen Fisher Panel
Cointegration Test proposed by Johansen (1988). In both tests, the null hypothesis is that
cointegration does not exist. I implemented both tests for all models with non-stationary
dependent variables and all p-values were less than 0.05. Therefore, based on the results
of both tests, the null hypothesis is rejected, which means that a cointegration
relationship exists among the variables. In other words, the error terms are stationary,
and the results of the regressions are not spurious. Another econometric issue that arises
here is that the error terms are autocorrelated and also they do not have constant
variance, which shows the existence of heteroskedasticity. To overcome autocorrelation and
heteroskedasticity, Newey-West Heteroskedasticity and Autocorrelation Consistent (HAC)
standard errors are used. In other words, since I worry that there might be some serial
correlation in the error terms even after controlling for fixed effects and endogeneity of
remittances, I adjust standard errors to account for heteroskedasticity and
autocorrelation by using autocorrelation HAC standard errors. Another issue that needs to
be addressed is that whether standard errors should be adjusted for clustering. There is
no cluster in the population of interest that is not represented in the sample. Moreover,
except for the case of Ordinary Least Squares (OLS) results which are provided in the
tables only for comparison purposes, fixed effects are included in the regressions and
there is no need to adjust standard errors for clustering. (Abadie et al., 2017)
Remittances may be endogenous to education or health outcomes in the remittance-receiving
countries. The endogenous relationship between workers' remittances received and schooling
decisions or health outcomes can be explained via three reasons. First, there exists a
reverse causality between human capital (education attainment and health outcomes) and
remittances. An individual may decide to migrate and send remittances because he or she
has school-age or sick and undernourished children, and in turn, remittances affect
educational investment or health outcomes by loosening liquidity constraints. The decision
to live outside the country and send remittances is determined simultaneously with the
decision regarding health and education expenditures. Second, there exist unobserved
characteristics included in the error terms that may be correlated with both the decision
to send remittances and the decision to send children to a school, or how much the
household spends on their nutrition and health (e.g. ability or ambition). Third,
measurement error is another source of endogeneity. Officially recorded remittances do not
include remittance in kind, unofficial transfers through kinship or through informal means
such as hawala operators, friends, and family members. The negative impact of transactions
costs on remittances encourages migrants to remit through informal channels when costs are
high. Transfer costs are higher when financial systems are less developed. Evidence from
household surveys also shows a sizable informal sector (Freund and Spatafora, 2008). Since
poor countries usually are less financially developed, migrants from poor countries are
more likely to remit through informal channels. Because income is also correlated with
human capital investment, measurement error is also one of the sources of endogeneity.
Therefore, the least squares estimates of the impact of remittances may be biased as
remittance is endogenous. The traditional way, which is followed in this paper, is to
resolve the endogeneity problem by using instrumental variables. In the following, the
instruments suggested by other researchers are discussed and then I introduce the
instruments that are used in this paper. Three kinds of instruments are proposed by
scholars. The first category of variables is related to remittance-receiving countries.
The main problem with using these instruments is that they can easily be correlated with
education, health or labor supply of the same country in a way other than through
remittances or covariates. Therefore, they can be invalid instruments. The second category
of variables is related to the cost of remittances (e.g. the number of branches of Western
Union). These instruments are usually strong and valid, but data on these variables are
mainly unavailable for most developing countries. The third category of variables is
related to remittance-sending countries. Since these variables are not related to
remittance-receiving countries, after controlling for some covariates, they are valid and
strong. However, the main problem is that each remittance-receiving country receives
remittances from many remittance-sending countries, and due to lack of information on
bilateral remittances, the weights of remittance-sending countries are unknown. Aggarwal
et al. (2011) use economic conditions in the top remittance-source countries as
instruments for the remittances flows. They argue economic conditions in the remittance-
source countries are likely to affect the volume of remittance flows that migrants are
able to send, but are not expected to affect the dependent variables in the remittance
receiving countries in ways other than through its impact on remittances or covariates.
However, because bilateral remittance data are largely unavailable, they identify the top
remittance-source countries for each country in the sample, using 2000 bilateral migration
data. The dataset identifies the top five OECD countries that receive the most migrants
from each remittance-recipient country. They construct instruments by multiplying the per
capita GDP, the real GDP growth, and the unemployment rate, in each of the top five
remittance-source countries by the share of migration to each of these five countries. The
technique used in this paper is similar to Aggarwal et al. (2011). However, I use an
estimation of bilateral remittances and use them as weights of remittance-sending
countries. In this research, I introduce three instruments that are correlated with
remittances and uncorrelated with the dependent variables unless through explanatory
variables. Workers' remittances, by definition, are money sent by migrants from host
countries (remittance-sending countries) to their home countries (remittance-receiving
countries). The value of remittances hinges on both remittance-sending and remittance-
receiving countries economic variables. Since the dependent variables belong to
remittance-receiving countries, in order to ensure the instruments are valid, we should
select a number of economic variables from remittance-sending countries. Three variables
used in this research as instruments are per capita GNI, unemployment rate, and real
interest rate. If the remittance-sending country's per capita GNI increases, it means
migrants' income has increased, which means they have more money available to spend and
remit. Therefore, it can be expected that remittances increase in response to a rise in
the remittance-sending country's per capita GNI. If the unemployment rate goes up in the
remittance-sending country, some migrants will lose their jobs, and the total remittances
sent by migrants will decrease. If the real interest rates go up in the remittance-sending
country, migrants have more incentive to invest in the host country rather than the home
country, and they will remit less. Table 3 shows the results of regressing per capita
remittances on these three instrumental variables while in each column different
covariates have been used. Note that in all seven columns the parameter estimate for the
impact of per capita GNI in remittance-sending countries on remittances is significant and
positive, the parameter estimate for the impact of unemployment rate and real interest
rates in remittance-sending countries on remittances is significant and negative. The IMF
provides workers' remittances data annually. Data are available at the aggregate level for
each country. Unfortunately, the IMF does not provide bilateral remittance data. Bilateral
remittance means how much money a remittance-receiving country receives from each specific
remittance-sending country. Therefore, although we know how much remittance each
remittance-receiving country receives in any year in total, we do not know how much of the
received remittances comes from a specific remittance-sending country. Fortunately, the UN
has provided a comprehensive bilateral migration data from 1990 to 2015. This means we
know how many immigrants live in each host-country, and we also know how many of them are
from each specific home-country. I used this dataset,4 per capita GNI of remittance-
sending countries, and per capita GNI of remittance-receiving countries to estimate
bilateral remittances. I then use estimated bilateral data to construct weighted averages
of per capita GNI, unemployment rate, and real interest rate of remittance-sending
countries. These weighted average indicators are used as instruments to address the
endogeneity of remittances. Before discussing the results of the regressions, I will
provide some evidence about the correctness of the estimated bilateral remittance data.
Data on bilateral remittances are mostly unavailable. Even where bilateral remittances are
reported, they may not be accurate, because funds channeled through international banks
may be attributed to a country other than the actual source country (Ratha, 2005). One
reason why bilateral remittance data is inaccurate is that financial institutions that act
as intermediaries often report funds as originating in the most immediate source country.
For example, the Philippines tends to attribute a large part of its remittance receipts to
the United States because many banks route their fund transfers through the United States
(Ratha, 2005). Only a few papers have used bilateral remittances data. and only for
limited recipient-country sender-country pairs (Lueth and Ruiz-Arranz, 2008; Frankel,
2011; Docquier et al., 2012). I compare the estimated bilateral remittances used in this
paper with the corresponding part of the datasets they used in their studies. The actual
data consists of 12 receiving countries, 16 remittance-sending countries, and 1744
observations.5 The Pearson Correlation Coefficient between actual data and estimated data
is 0.666 and is statistically significant, indicating there is a strong positive linear
correlation between actual data and estimated data. This study uses Kolmogorov-Smirnov's
two-sample test to check if the distribution of the two samples is the same or not. The
null hypothesis is that the two distributions are not statistically different from each
other. Using the panel data, the p-value for the test is 0.17, and I fail to reject the
null. Two main concerns of using instrumental variables method, to address the problem of
endogeneity, are validity and strength of the instruments. The reason that in this paper
bilateral remittances are estimated, and economic variables related to remittance-sending
countries are used is to guarantee the validity of the instruments. More specifically,
selecting economic variables from remittance-sending countries, rather than from
remittance-receiving countries, as instruments is to ensure the validity of instruments.
My identifying assumption is that per capita GNI, unemployment rate, and real interest
rate in remittance-sending countries do not affect health outcomes, educational
attainment, and labor force participation in remittance-receiving countries other than
through remittances, per capita GDP of remittance-receiving countries, or other covariates
included the regressions. The other concern about the instruments is whether they are
strong or not. The whole process of estimating bilateral remittances and use them as the
weights of remittance-sending countries is to ensure that instruments are strong. To
investigate the strength of the instruments, first stage regressions are examined. The
results of the first stage regressions are provided in Table 3. Note that all F-statistics
for weak instruments are greater than 50, which indicates the instruments are very strong.
There is a clear advantage in using estimated bilateral remittances to construct the
instruments over using top 5 or 10 remittance-sending countries (the method used by other
researchers). This advantage can be demonstrated by the substantial improvement in the
F-statistic for weak instruments of this paper and similar papers. For example,
F-statistic for two of the main instruments used in this paper, GNI per capita and
unemployment rate in remittance-sending countries, are 342 and 98 respectively. These two
F-statistics are remarkably higher than F-statistic in similar studies which use GNI per
capita and unemployment rate in just top one or three or five remittance-sending countries
as instruments.

<h>RESULTS</h>
-------

This section is divided into four subsections. At first, I investigate impacts of
remittances on health outcomes in Tables 4–6 and gender-specific impacts of remittances on
health outcome in Tables 7 and 8. Then, I explore the impacts of remittances on education
in Tables 9–11 and gender-specific impacts of remittances on education in Tables 12–14.
Afterward, I look into the impact of remittances on HDI in Table 15. Finally, I examine
the impacts of remittances on labor supply in Table 16. In all regressions, the results of
the IV approach are reported alongside the results of the OLS model and Fixed Effect (FE)
model. FE model and OLS model are similar in all aspects except one. Unlike OLS model, FE
model includes region-specific effects and addresses time-invariant cross-country effects.
However, both OLS and FE results are inconsistent and biased. They are presented in this
paper for comparison purposes. To address both endogeneity and time-invariant cross-
country effects simultaneously, all IV estimates also include region-specific effects.

<hs>  Remittances and health</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

This study closely follows the literature on the choice of health measurements. Four
categories of health measurements are used here as dependent variables: health
expenditures, life expectancy at birth, nutrition status, and child mortality rates. Per
capita out-of-pocket health expenditure and per capita total health expenditure are the
variables representing health expenditures. Undernourishment prevalence, depth of food
deficit, and prevalence of stunting are three variables representing nutrition
measurements. Neonatal, infant, and under-five mortality rates represent child mortality
rates. The estimates for the impacts of remittances on out-of-pocket per capita health
expenditures, per capita total health expenditures, and life expectancy are presented in
Table 4. For many countries, just one year of data is available, and for using country-
specific effect, those countries had to be dropped from the regression. Due to this data
limitation, this study controls for region-specific effect rather than country-specific
effect. However, for those cases where more data are available, at least two years of data
for each remittance-receiving country, it is possible to control for country-specific
effect. As a robustness check, I use country-specific effect in those regressions and
investigate the impact of remittances on health outcomes. The results are the same as
regressions with region-specific dummies in terms of sign and significance of remittances,
but the magnitudes are slightly different.6 In the first regression, per capita out-of-
pocket health expenditure is used as the dependent variable. Population over 65 and urban
population share are used as explanatory variables alongside per capita remittances and
per capita GDP. Both OLS and FE models underestimate the impacts of remittances on health
expenditures and the effect captured by the IV is larger than the effects captured by the
OLS or the FE. The results of IV regression suggest that, on average, a 10% increase in
per capita remittances and per capita GDP will lead to a 1.5% and 6.4% increase in per
capita out-of-pocket health expenditure, respectively. In the second regression, per
capita total health expenditure is used as the dependent variable. The results of IV
regression suggest that, on average, a 10% increase in per capita remittances and per
capita GDP will lead to a 1.1% and 8.9% increase in per capita total health expenditure,
respectively. Note that the impact of per capita remittances on per capita total health
expenditure is smaller than the impact of per capita remittances on per capita out-of-
pocket health expenditure. The reason is that total health expenditure is the sum of
private and public health expenditure and remittances have almost no effect on public
health expenditure. In the third regression, life expectancy at birth is used as the
dependent variable. The results of IV regression suggest that, on average, a 10% increase
in per capita remittances and per capita GDP will lead to a 0.3% and 0.4% increase in life
expectancy at birth respectively. The impacts of per capita remittances, per capita GDP,
alongside other variables, on nutrition variables are provided in Table 5.
Undernourishment prevalence, depth of food deficit, and prevalence of stunting are used as
the fourth, fifth, and sixth measurements of health outcomes. Due to restrictions in the
availability of data, the number of observations in each regression varies considerably.
For example, in the regression with undernourishment prevalence as the dependent variable,
the number of observations is 1629, but in the regression with prevalence of stunting as
the dependent variable, the number of observations is 412. Food production index and urban
population share are used as explanatory variables alongside per capita remittances and
per capita GDP. The results of IV regressions suggest that, on average, a 10% increase in
per capita remittances and per capita GDP will lead to, respectively, a 1.5% and 4.3%
decline in undernourishment prevalence, a 1.9% and 5.9% decline in depth of food deficit,
and a 1% and 2.7% decline in prevalence of stunting. Note that the magnitude of IV
coefficients for per capita remittances are substantially larger than those from the OLS
and FE estimations in all three regressions which means OLS and FE models underestimate
the impacts of workers' remittances on undernourishment prevalence, depth of food deficit,
and prevalence of stunting. The impacts of per capita remittances, per capita GDP,
alongside other variables, on child mortality rates are provided in Table 6. In order to
investigate the impact of remittances on child mortality rate, health expenditure to GDP
ratio, urban ratio, and newborns protected against tetanus are chosen as control
variables. Since high-income countries are primary funders of the World Health
Organization (WHO), their economic conditions can affect WHO's budget, which in turn
affects child mortality rates in developing countries through different global vaccination
programs implemented by WHO. Controlling for the variable newborns protected against
tetanus can assure the validity of the instruments used in the IV regressions. Both OLS
and FE models underestimate the impacts of remittances on reducing child mortality rates.
Remittance has negative and statistically significant effects on child mortality rates.
Based on the IV results, on average, a 10% increase in per capita remittances causes a 1%
decrease in neonatal mortality rate, a 1.7% decrease in infant mortality rates, and a 1.9%
decrease in under five mortality rates. Also, on average, a 10% increase in per capita GDP
leads to a 3.9% decrease in neonatal mortality rates, a 4.2% decrease in infant mortality
rates, and a 4.7% increase in under five mortality rates. Gender-specific data are
available only for four health outcome variables: life expectancy at birth, prevalence of
stunting, infant mortality rate, and under-five mortality rate. Table 7 provides the
gender-specific impacts of per capita remittances on life expectancy at birth and
prevalence of stunting. Remittance has positive, statistically significant, and almost
similar effects on male and female life expectancy. On average, a 10% increase in per
capita remittances causes a 0.3% increase in male and female life expectancy at birth.
Also, on average, a 10% increase in remittances leads to a 1.3% decrease in male and 1.2%
decrease in female prevalence of stunting. Table 8 provides the gender-specific impacts of
per capita remittances alongside per capita GDP, per capita health expenditure, urban
population share, and newborns protected against tetanus on infant mortality rates and
under-five mortality rates. There are negligible differences on impacts of remittances on
child mortality rates between two genders: on average, a 10% increase in the amount of per
capita remittances leads to a 1.31% and 1.35% reduction in infant mortality rates for
males and females, respectively. Also, on average, a 10% increase in the amount of per
capita remittances leads to a 1.43% and 1.49% reduction in under 5 mortality rate for
males and females, respectively. These results show that when households in developing
countries receive remittances from their family members living abroad, they spend the
received money almost equally on the health status of their boys and girls. As we will
see, this is not the case for the impact of remittances on education as remittances
increase the female education more than male education.

<hs>  Remittances and education</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~

In all regressions with education measurements as dependent variables, per capita
remittances, per capita GDP, labor force participation rate, and government expenditure on
education are used as explanatory variables. Pre-primary enrollment rate, primary
enrollment rate, and secondary enrollment rate are the first three education measurements.
The impacts of per capita remittances on these three variables are displayed in Table 9. A
rise in workers' remittances (which is represented by per capita remittances) or in income
measurement (which is represented by per capita GDP) can loosen the budget constraints for
households in developing countries and motivate them to invest more in their children's
education. The results provided in Table 9 show how worker’ remittances can increase
children's school attendance in developing countries. On average, a 10% rise in per capita
remittance increases pre-primary and secondary enrollment by 3.5% and 0.6%, respectively.
However, based on the IV model, while a 10% rise in per capita remittance increases
primary enrollment by 0.16%, this impact is not statistically significant. Also, on
average, a 10% rise in per capita GDP increases pre-primary, primary, and secondary
enrollment by 6.6%, 0.7%, and 3.2%, respectively. When labor force participation
increases, parents have more incentive to invest in their children's education. If parents
predict that their children, especially their girls, will not enter the job market, then
they will have less incentive to spend on their children's education. Therefore, it is
expected that the labor force participation rate has a positive impact on education. On
average, a 10% rise in the labor force participation rate increases pre-primary, primary,
and secondary enrollment by 15.9%, 4.8%, and 3.5%, respectively. Also, when the government
expenditure on education increases, the marginal rate of return on households' investment
in education increases. The increased marginal rates of returns, in turn, promote
households to spend more on their children's education. On average, a 10% rise in
government expenditures on education increases pre-primary, primary, and secondary
enrollment by 3.8%, 0.6%, and 2.5%, respectively. The substantial difference between the
impacts of per capita remittances on pre-primary enrollment rate, primary enrollment rate,
and secondary enrollment rate can be explained by considering the mean these variables:
39.3%, 100.6%,7 and 60.7%, respectively. Households in developing countries consider pre-
primary education as a luxury commodity. However, they consider primary education, which
is required in many countries, as a necessity. Therefore, the elasticity of pre-primary
enrollment rate with respect to per capita remittances or per capita GDP is expected to be
higher than the elasticity of primary enrollment rate. However secondary education is less
of a necessity in comparison with primary education, and tertiary education is less of a
necessity in comparison with secondary education. Therefore, it is reasonable that
secondary enrollment rate has a higher elasticity than primary enrollment rate, and
tertiary enrollment rate has a higher elasticity than secondary enrollment rate. The
impacts of per capita remittances on tertiary enrollment rate, primary age out of school
rate, and private primary enrollment rate are shown in Table 10. The results presented in
Table 10 show that, on average, a 10% rise in remittance per capita increases tertiary
enrollment rate by 1.1%. However, based on the IV model, while a 10% rise in per capita
remittance decreases out of school rate of primary age children by 1%, this impact is not
statistically significant. The last dependent variable used in Table 10 presents the
impact of workers' remittances on the quality of children's education rather than the
quantity. On average, a 10% rise in per capita remittances increases enrollment in private
primary schools by 2.8% which means that a rise in remittances leads to a net substitution
from public to private primary schools, hence increasing the quality of children's
education. In contrast, a rise in per capita GDP leads to a net substitution from private
to public primary schools. One explanation is that as per capita GDP of developing
countries increase, the quality of public schools also increase and parents will have less
incentive to send their children to private schools. As Table 11 shows, on average, a 10%
rise in per capita remittance increases primary completion rate by 0.6% and secondary
completion rate by 0.9%. Once again, the difference in the impacts of per capita
remittances on these two measurements of education can be explained by taking into account
the average primary completion rate and lower secondary completion rate: 80% and 60%,
respectively. Households in developing countries consider primary education a necessity
and secondary education as less of a necessity than a luxury commodity. Therefore, it is
reasonable that secondary completion rate has higher elasticity than primary completion
rate with respect to per capita remittances and with respect to per capita GDP. Based on
the descriptive statistics, boys' average primary enrollment rate is 103.4%8 and girls'
average primary enrollment is 97.4%. This means the average households' investment in
girls' primary education is less than their investment in boys' primary education in
developing countries. Therefore, the marginal rate of return on primary education is
higher for girls than boys. Hence, the inflow of remittances, which loosens the budget
constraints for households in developing countries, is invested more heavily in girls'
primary education than boys. This, in turn, raises the primary gender parity index, though
just by a small amount. On average, a 10% rise in per capita remittance increases the
primary gender parity index by 0.2%. This impact is statistically significant in all three
models: OLS, FE, and IV. Workers' remittances increase the gender parity index. The rise
in gender parity index means when households in developing countries receive remittances
from the migrants, they spend a higher proportion of it on girls' primary education than
on boys. This is particularly important because, as Bansak and Chezum (2009) state, if
remittances do affect human capital positively, then not only will remittances affect
long-run growth in developing countries, but the opportunities for women should improve as
the female population becomes more educated in these countries. Table 12 provides gender-
specific effects of per capita remittances, per capita GDP, government expenditure on
education, and gender-specific labor force participation rate on male and female pre-
primary enrollment rates and primary enrollment rates. On average, a 10% increase in per
capita remittances increases male and female pre-primary enrollment rates by 3.4% and
3.5%, respectively. In contrast, while per capita remittance has no statistically
significant impact on male primary enrollment rate, on average, a 10% increase in per
capita remittances increases female primary enrollment rate by 0.3%. This asymmetric
impact of remittances on female and male primary enrollment rate is in line with the
positive impact of remittances on the gender parity index of primary education. There is a
remarkable heterogeneity between the impact of the male labor force participation rate on
male education and the impact of the female labor force participation rate on female
education. While male labor force participation has no effect on male education
investment, female labor force participation has a positive and significant effect on
female education investment. On average, a 10% increase in the female labor force
participation rate increases female pre-primary and primary enrollment by 3.1% and 0.6%,
respectively. The impacts of the same explanatory variables on secondary and tertiary
enrollment rates are provided in Table 13. Results provided in Table 13 show that per
capita remittance has a greater impact on the female secondary and tertiary enrollment
rates than on the male rates. On average, a 10% increase in per capita remittances
increases male and female secondary enrollment by 0.7% and 0.9%, respectively. On average,
a 10% increase in per capita remittances increases male and female tertiary enrollment by
0.6% and 1.3%, respectively. The impacts of the explanatory variables on male and female
primary and secondary completion rates are provided in Table 14. The results provided in
Table 14, confirm that remittance has a greater effect on the female primary and secondary
completion rates than on male rates. On average, a 10% increase in per capita remittances
increases the male and female primary completion rates by 0.5% and 0.9%, respectively. On
average, a 10% increase in per capita remittances increases the male and female lower
secondary completion rate by 0.8% and 1.2%, respectively. Comparing the elasticities
obtained for male and female education with respect to per capita remittances in Tables
12–14 shows that households in developing countries, upon receiving remittances, invest in
girls' education more than boys' education.

<hs>  Remittances and HDI</hs>
  ~~~~~~~~~~~~~~~~~~~

As a robustness check for the impact of remittances on human capital, I examine the effect
of remittance on HDI in developing countries. Table 15 provides the impacts of per capita
remittances, per capita GDP, government expenditures on education, and per capita health
expenditures, on total, male, and female HDI. As Table 15 shows, on average, a 10% rise in
per capita remittances increases total HDI, male HDI, and female HDI by 0.35%, 0.3%, and
0.4%, respectively. Note that only limited amounts of gender-specific HDI data are
available. The number of observations in the first regression is 1069, and in the second
and third regressions, 394 and 393, respectively. The positive impact of remittance on HDI
confirms previous findings in this paper. Workers' remittances do improve human capital in
developing countries.

<hs>  Remittances and labor force participation</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

This section examines the impact of workers' remittances on the labor force participation
rate in the remittance-receiving countries. Remittances can affect labor force
participation in remittance-receiving countries mainly through two channels: human capital
and reservation wages. As stated by Amuedo-Dorantes and Pozo (2006) remittances and the
error term in equation (1) may be correlated. Remittances may be endogenous and their
coefficient estimates may be biased. There are three potential sources for this
endogeneity. Omitted variable bias may exist if remittances are related to wealth which,
in turn, may be correlated to the labor supply by the recipient. Additionally, there is
the potential of reverse causality as labor supply may influence migrants' decisions to
send remittances home. The third source of endogeneity can be measurement errors.
Therefore, in this section, I use the same five instrumental variables to address the
endogeneity of remittances. So far, we have concluded remittances increase human capital,
especially health and education outcomes, in developing countries. On the one hand,
increases in human capital can increase labor force participation. On the other hand,
remittances, as a non-labor source of income, increase reservation wages in developing
countries. Increases in the reservation wage can cause a reduction in the labor force
participation rate. Therefore, the net impact of remittances on labor supply (labor force
participation) is a priori unclear. The important question is: does the rise in the
reservation wage and its negative impact on labor force participation outweigh the
positive impact of remittances on labor force participation through raising human capital?
If so, are the impacts of remittances on male and female labor force participation rates
symmetric? The impacts of remittances on total, male, and female labor supply are provided
in Table 16. In the IV model provided in Table 16, I use instruments to address the
endogeneity of workers' remittances and control for the level of income, education, the
ratio of the population living in urban areas, and geographic region. The results of the
impact of remittances on labor force participation rate suggest that, on average, a 10%
increase in remittances leads to a 0.17% decline in total labor force participation rate,
a 0.03% decline in the male labor force participation rate, which is not statistically
different than zero, and a 0.33% decline in the female labor force participation rate.
These results show that while workers' remittances have no impact on the male labor force
participation rate, they reduce the female labor force participation rate in developing
countries. There is an enormous heterogeneity in labor force participation between men and
women in developing countries. This heterogeneity is clearer when we review the
descriptive statistics provided in Table 2. While average labor force participation for
men is 76.6% in developing countries, it is just 50.9% for women. Due to cultural features
of many developing countries, reservation wage for women is more sensitive to non-labor
income than reservation wage for men. Therefore, upon receiving a greater amount of
remittances some working-women will stop working. This is not the case for men in
developing countries.

<h>CONCLUSION</h>
----------

Remittances can increase investment in human capital. This impact is especially important
since human capital is a crucial factor in the promotion of growth in developing countries
in the long-run. This paper uses a dataset on workers' remittances, health outcomes, and
educational attainment of 122 developing countries from 1990 to 2015 and an innovative
instrumental variables estimation strategy to examine the impact of workers' remittances
on human capital and labor supply in the developing world. Also, the gender-specific
effects of remittances on health, education, HDI, and labor force participation are
investigated. The results obtained in this paper show that remittances have an improving
and statistically significant impact on health outcomes in developing countries. I use
instruments to address the possible endogeneity of workers' remittances and control for
level of income, some covariates, and geographic region. The results of the impact of
remittances on health outcomes suggest that, on average, a 10% increase in per capita
remittances will lead to a 1.5% increase in out-of-pocket per capita health expenditures,
a 1.1% increase in total per capita health expenditures, 0.3% increase in life expectancy
at birth, 1.5% decline in undernourishment prevalence, 1.9% decline in depth of food
deficit, and 1% decline in prevalence of stunting. Also, remittances have a strong and
statistically significant effect on reducing child mortality rates in developing
countries. On average, a 10% increase in per capita remittances will lead to a 1% decline
in neonatal mortality rate, 1.7% decline in infant mortality rate, and 1.9% decline in
under-five mortality rate. The gender-specific results show that the effects of workers'
remittances on reducing infant and under-five mortality rates are almost the same for male
and female children. Remittances also have a positive and statistically significant impact
on education in the developing countries. I use instrumental variables to address
endogeneity of workers' remittances and control for the level of income, government
expenditures on education, labor force participation, and geographic region. The results
of the impact of remittances on education outcomes suggest that, on average, a 10%
increase in per capita remittances will lead to a 3.5% increase in pre-primary enrollment
rate, 0.7% increase in secondary enrollment rate, and 1.1% increase in tertiary enrollment
rate. Remittances not only have a positive effect on enrollment rates but also have a
positive effect on quality of education: on average, a 10% increase in per capita
remittances will lead to a 2.3% increase in enrollment in private primary schools. In
addition to raising the enrollment rate, remittances increase school completion rates: on
average, a 10% increase in per capita remittances will lead to a 0.6% increase in primary
completion rates and 0.9% increase in secondary completion rates. Unlike the impacts of
remittances on reducing child mortality rates which were symmetric between genders,
remittances improve girls' education outcomes more than boys. On average, a 10% increase
in per capita remittances will lead to a 0.2% increase in the primary gender parity index,
the ratio of girls to boys enrolled at the primary level. On average, a 10% increase in
per capita remittances will lead to a 0.3% increase in girls' primary enrollment rate
while it has no statistically significant effect on boys' primary enrollment rate. These
results are in compliance with the positive effect of remittances on primary gender
parity. Also, on average, a 10% increase in per capita remittances will lead to a 1.3%
increase in girls' tertiary enrollment rate while it has no statistically significant
effect on boys' tertiary enrollment rate. The positive effect of remittances on girls'
education is greater than the positive effect of remittances on boys' education in all
case of school completion rates: 10% increase in per capita remittances rises male and
female primary completion rate by 0.5% and 0.9%, respectively and rises male and female
lower secondary completion rate by 0.8% and 1.2%, respectively. Since remittances improve
health and education outcomes in developing countries, it is expected to have a positive
impact on HDI as well. On average, a 10% increase in per capita remittances will lead to a
0.3% and 0.4% increase in male and female HDI, respectively. The net impact of remittances
on labor force participation is a priori unclear. On the one hand, workers' remittances
can increase human capital investments of poor households, hence increasing the labor
supply. On the other hand, remittances can loosen budget constraints, raise reservation
wages, and, through the income effects, reduce the labor force participation of
remittance-receiving individuals. The results obtained in the last section of this paper
show that remittances have a negative and statistically significant impact on labor force
participation in developing countries. I use instrumental variables to address the
possible endogeneity of workers' remittances and control for the level of income,
education, the percentage of population living in urban area, and geographic region. The
results of the impact of remittances on labor force participation suggest that, on
average, a 10% increase in per capita remittances will lead to a 0.17% decrease in labor
force participation. The results of gender-specific effects of remittances on labor force
participation can be more informative. While remittances have no statistically significant
effect on male labor force participation, they reduce female labor force participation: on
average, a 10% increase in per capita remittances will lead to a 0.3% decline in female
labor force participation. This study contributes to the literature in a number of ways.
First, this paper uses data from 122 developing countries over the period from 1990 to
2015. I am not aware of any other studies which explore the impact of remittances on human
capital and labor supply and uses such a large dataset. Second, this study uses an
innovative new approach for building instruments to address the endogeneity of
remittances. This study estimates bilateral remittances uses them to create weighted
indicators of remittance-sending countries. These weighted indicators are used as
instruments for remittance inflow to remittance-receiving countries. selecting economic
variables from remittance-sending countries, rather than from remittance-receiving
countries, as instruments is to ensure the validity of instruments. Using estimated
bilateral remittances and to construct the instruments is to ensure that instruments are
strong. This novel approach to instruments can be applied to address the endogeneity
problem while exploring the impact of remittances on many socioeconomic variables such as
education, health, labor supply, poverty, inequality, growth, and financial development.
Moreover, this approach can be used in both country-level studies and household-level
studies. Finally, this study, in addition to investigating the overall impact of
remittances on human capital and labor supply, explores the impacts of remittances on male
and female human capital and labor supply using a wide range of gender-specific variables.
This allows researchers to compare the impacts of remittances by gender. In terms of
policy recommendation, the high-income countries should take further steps to reduce the
current transaction costs of remitting money to remittance-receiving countries. Based on
Remittance Prices Worldwide (RPW) reports, the average global cost of remittances went
down from 9.12% in the first quarter of 2012 to 7.52% in the third quarter of 2015.
Unfortunately, since the third quarter of 2015, the cost of remittances has not been
reduced any further. The global cost of remittances in the first quarter of 2017 was
7.45%, staying 4.45 percentage point above the 3% UN SDG goal. The high transaction costs
act as a type of tax on emigrants from developing countries who are often poor and remit
small amounts of money with each remittance transaction. Lowering the transaction costs of
remittances would not only encourage a larger share of remittances to flow through formal
financial channels but will also help to improve health and education outcomes in
developing countries.


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<ART>The long-term consequences of youth housing for childbearing and higher education
================================================================================

Authors: Cecilia Enström Öst, Mats Wilhelmsson
DOI: 10.1016/j.jpolmod.2019.05.008
Year: 2019  |  Pages: 845-858
ASJC codes: 2002
Keywords: Childbearing, Higher education, Housing market, Propensity score matching, Youth housing

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

The lack of housing in areas where young adults have greater opportunities to study and get work complicates young adults’ entry into the adulthood. Difficulties in accessing housing may therefore delay childbearing and may negatively have an effect on education opportunities. To increase housing accessibility, some municipalities have earmarked apartments for young adults. These “youth dwellings” are criticized for being small and not necessarily facilitating family formation and fertility, better suiting students’ needs. We have in this paper compared the long-term pattern of childbearing and education for young adults that entered their housing market through small cheap youth housing with those youngsters that received a rental apartment from the ordinary housing stock. To be able to draw the conclusion that differences in fertility and educational pattern between these two groups comes from the different housing situation and not from differences in in preferences when it comes to childbearing or individual prerequisites for higher education, we have used a geocoded data and information on the individual's family background as well as a matching technique to create a comparison group that are similar to the treatment group in several aspects. The present results indicate that building affordable housing that is small and space efficient is sufficient and positive if the aim is to promote higher education. Affordable housing is on the other hand not enough to promote childbearing, instead, it seems to inhibit childbearing until there is a possibility of moving on in the housing career. Our result also indicates that the next step need not necessarily be homeownership, as earlier research has indicated. Entering the housing market via youth housing and then being able to move on to rental accommodation in the ordinary housing market also seems to have a positive effect on overall childbearing, although moving to cooperative housing or owned housing has an even larger effect.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The increase in adult children living with their parents has raised important questions
regarding household formation. Furthermore, the lack of housing in areas where young
adults have greater opportunities to study and get work complicates young adults’ entry
into the housing market. Earlier research has found that housing and childbearing are
closely connected and difficulties accessing the housing market may possibly lead to
delayed childbearing (see, e.g., Mulder, 2006, 2013; Pinnelli, 1995; Castiglioni & Dalla
Zuanna, 1994; Krishnan & Krotki, 1993; Clark, 2012) and may negatively influence education
opportunities (see, e.g., Cunningham, Harwood, & Hall, 2010; Dworsky, 2008; Garriss-Hardy
& Vrooman, 2005; Crowley 2003; Conley, 2001; Rosenbaum, 1995). But is affordable housing
sufficient to promote childbearing and education? Leaving the parental home occurs for
various reasons, the role of available housing likely differs for each reason. Young
adults who want to leave home for education have little latitude for postponement and are
likely to move even if they have to accept substandard housing (Mulder, 2006, p. 406).
Those who want to leave the parental home for household formation have more latitude to
wait until they have found suitable or/and affordable housing. For example, it has been
demonstrated that higher housing costs are associated with lower probabilities of leaving
the parental home to live with a partner, an association not found for those leaving the
parental home to live alone (Mulder & Clark, 2000). Family formation has been demonstrated
to be connected to homeownership tenure. Studies have also found that the decisions to
become a homeowner and have children are made simultaneously (Malmberg, 2010, Enström Öst,
2012a, Kulu & Steele, 2013). Furthermore, it has been demonstrated that the likelihood of
having children is greater for homeowners and that the transition to first-time
homeownership often occurs in anticipation of parenthood (Mulder & Wagner, 2001; Feijten &
Mulder, 2002, Mulder, 2006, Kulu, 2008, Holland, 2012). However, having small amounts of
equity in one´s home reduces the ability to realize a desired move (Ferreira, Gyourko, &
Tracy, 2010). An affordable housing market may enable smooth entrance into the housing
market, perhaps via a small cheap apartment, enabling later progress in the housing career
to higher-quality housing (Mulder, 2006, 2013). If young people succeed in leaving the
parental home and enter the housing market in a small dwelling, this may positively affect
childbearing if subsequent access to high-quality housing is easy. However, if such
housing is scarce, prices are high, and/or mortgage providers are strict, young people
might postpone childbearing until they find a house suitable for family formation, which
may reduce the number of children born (cf. Chiuri & Jappelli, 2003). Similarly, Vignoli,
Rinesi, and Mussino (2013) find that women who feel more secure about their housing
conditions are more likely to plan to have their first child. Simon and Tamura (2009) and
Clark (2012) have explicitly investigated the effect of housing costs on childbearing.
Both studies show that first birth is significantly delayed in an expensive housing
market. Liu and Clark (2016) demonstrates that an increase in the cost of renting is
predicted to decrease the number of children born by renting households. However, the
effect of higher house price is ambiguous and depends on the initial holdings of housing
and the willingness to substitute between children and other goods. The housing market in
Sweden, especially in the capital Stockholm, is increasingly difficult for young adults to
enter (Bokriskommittén, 2014; Swedish union of tenants, 2015). This market is
characterized by increasing prices and housing costs and by housing construction that has
lagged behind population growth (The Swedish National Board of Housing, Building and
Planning, 2013). Queues to obtain rental apartments are growing and cooperative apartment
prices are high. Studies indicate that a generation of young people may have little or no
chance of accessing the housing market unless they are rich, well paid, or/and have
generous and wealthy parents (cf. Enström Öst, 2012b). Fertility research commonly relates
the relatively high Swedish fertility to the characteristics of the Swedish welfare regime
that, for example, may promote female labour-market attachment by making it easier to
combine work and family life (see, e.g. Andersson & Scott, 2007). However, along with
indications of an inaccessible housing market for young people, the average age at which
women bear their first child has increased in Sweden by approximately one year over a
five-year period (cf. Andersson, 1999, 2000; Statistics Sweden, 2011). Recent years have
also seen reports of students in higher education being forced out of larger cities, such
as Stockholm, because of difficulties finding accommodation. To try to increase the
accessibility of the housing market, housing projects targeting young adults have been
started in Sweden. Several municipalities have earmarked small apartments for young adults
to help them compete for an access to rental apartments. By examining a housing project
for young adults in Stockholm, initiated as early as 1996, this study advances our
understanding of whether building small apartments for young adults may solve problems
related to housing shortage for young. This study will investigate the causal effects of
youth housing on higher education and parenthood. To our knowledge, no earlier studies
have this focus. The dataset for this study contains information on young people who
gained access to the housing market in 1996 via a particular youth housing project in
Stockholm. This study explores the development of their fertility pattern and education
level during a time period of 14 years after they entered the housing market and compares
them with the fertility and educational pattern of a matched group of young people similar
in several respects. Matching is used to evaluate the effect of youth housing by comparing
those young adults that moved into the youth house in 1996 with those young adults that
moved into an ordinary rental apartment the same time period. The goal of this matching
procedure is, for every young adult that moved into the youth house, to find at least one
young adult with similar observable characteristics against whom the effect of youth
housing can be assessed. With the data available for this project we can match on
explanatory variables five years before the youth house was defined. By this matching
procedure, it enables a comparison of outcomes among young adults moving into youth
housing and young adults that moves into the ordinary rental housing stock to estimate the
effect of youth housing reducing bias due to confounding. The present result indicates
that having access to small youth housing reduces the probability of becoming a parent.
However, if the rest of the housing market is mobile, i.e., enables young adults to move
on in their housing careers, the total effect on becoming parent is positive. The effect
from living in youth house on completing higher education is positive and independent of
the mobility of the rest of the housing market. This result confirms that the housing
market has repercussions for both the fertility and the educational patterns. The paper is
organized as follows: The next section discusses the theory of household formation and the
Swedish housing market during the study period and describes the studied youth housing
case. Section 3 presents the data and the empirical strategy and Section 4 presents the
results. The paper ends by presenting the conclusions and discussing the policy
implications of the present findings.

<hs>  Theory of housing and household formation</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

A large body of empirical work emphasizing the role of life course events on mobility,
such as leaving the parental home and get birth to a child (Clark & Dieleman, 1996).
Transition to life stages involving higher levels of commitment, such as parenthood, lead
to requirements for long-stay housing and to changing preferences over dwelling
attributes. However, desires for mobility may be prompted by a wide range of life events,
but desires cannot always be realized. Income and wealth constraints, transactions costs
that vary with tenure, social ties, the supply of dwellings and the functioning of the
housing and mortgage markets all affect whether a desired move will in fact be realized
(Kiel, 1994; Linneman & Wachter, 1989; Stein, 1995; Venti & Wise, 1984; Wheaton, 1990;
Helderman et al. 2004; Belot & Ermisch, 2009; Ermisch & Washbrook, 2012). Mulder (2006)
has explored the relationship between housing and household formation. Obviously, to move
from parental homes and form households, young people need somewhere to live. In a well-
functioning housing market, housing demand equals housing supply and all households can
access housing that meets their needs. However, housing prices, housing supply, and the
ability to obtain housing loans are limiting factors, especially for young adults who have
had limited time to accumulate savings for home down payments. Some young adults may
therefore postpone household formation if they cannot find suitable affordable housing.
The degree to which the availability of housing affects household formation, however,
probably depends on the urgency with which people want to form new households. Young
adults who need to move, for example, for work or higher education, might have little
latitude for postponement and may therefore move even though they must accept substandard
housing. However, those moving to cohabit, marry, or have children may have more latitude
to wait until they find suitable housing. Furthermore, young people who succeed in leaving
parental homes, for example, to live in student housing or smaller apartments, might still
postpone childbearing if they think housing of a certain quality is a precondition (see,
e.g., Ineichen, 1979, 1981; Ström, 2010). Lovenheim and Mumford (2013) also find a
statistically significant positive relationship between house price changes and fertility
for homeowners. However, no statistically significant negative relationship between house
price changes and fertility was found for renters. Dettling and Kearney (2014) find that
high housing prices have a negative effect on the fertility of renters but a positive
effect for home owners.

<hs>  The Swedish housing market</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~

The Swedish housing market has three dominant tenure forms: single-family housing,
cooperative multi-family housing, and multi-family rental housing. All rental housing
units are subject to rent control. In the case of cooperative housing, the property is
owned by a cooperative association. Each resident owns a share of the cooperative and
occupies an apartment with tenancy rights nearly as strong as those of full ownership.
Cooperative housing is traded on an ordinary free housing market and in practice is
regarded as a form of owner-occupied housing, although this is not precisely correct from
a judicial perspective. The standard of housing is generally high in Sweden, irrespective
of tenure type. The housing market in Sweden has undergone several gradual and substantial
changes in recent decades. The government housing policy of granting substantial subsidies
to all new housing construction changed in the early 1990s, and subsidies were gradually
phased out over a decade without being replaced with other investment incentives. This has
resulted in the low production of new housing of all types, and housing construction has
lagged population growth since 1991, as well as very high house prices and housing costs.
Swedish house prices increased by over 200% in the 17 years from 1996 to 2013, a period
when general consumer prices increased by only 60%. Furthermore, the price level of houses
in the first quarter of 2015 was 12 percent higher than in the first quarter of 2014.
However, this trend is even stronger in the market for cooperative apartments where the
prices was 17 percent higher during the first quarter of 2015 than in the corresponding
quarter of 2014 (The Swedish National Board of Housing, Building and Planning, 2015).
After the 1991 tax system reform, which led to sharply increased rents (Englund,
Hendershott, & Turner, 1995), the vacancy rate in the rental sector started to climb and
was quite high by 1998. Since then, vacancy rates have decreased and today several
counties in Sweden report a housing supply shortage (The Swedish National Board of
Housing, Building and Planning, 2015). In 2015, only 40 percent of Sweden’s young adults
lived in a home of their own. This is the lowest percentage ever measured in Sweden
(Swedish union of tenants, 2015). Furthermore, in 2015, 20% of young adults who had
children lived with a relative, in a rented room or in a student residence. Stockholm is
the largest and most dynamic regional housing submarket in Sweden; it is Sweden’s most
heterogeneous in terms of tenure forms, price variation, and neighbourhood structure,
though, from an international perspective, it is comparatively small, homogenous, and easy
for housing consumers to conceive of and analyse. The official recommendation to those who
want a rental apartment in inner Stockholm is to register as an applicant and stay on a
waiting list. Over the last two decades, in-migration to Stockholm has increased
substantially. With population growth substantially exceeding housing supply growth, the
Stockholm housing market is now suffering from a pronounced housing shortage (Andersson &
Söderberg, 2012). About 520,000 people were waiting for an apartment in Stockholm County
in January 2016 and the average waiting time for a rental apartment in the region exceeds
eight years. When it comes to student housing, approximately 80,000 students are waiting
for only 12,000 student dwellings.1

<hs>  “Youth house”</hs>
  ~~~~~~~~~~~~~

In 1995 a housing company in Stockholm decided to earmark an entire 150-apartment property
in inner Stockholm for young adults aged 18–25 years. These apartments had formerly been
earmarked for nurses working at the nearby hospital. The apartments were all small, i.e.,
30 square metres in floor area comprising one room with a kitchenette, and were deemed fit
for youth by the housing company. Earmarking these apartments for young adults therefore
required no major or costly renovations by the housing company. The property, located in
inner Stockholm and built in the 1950s, has been subject to no default-enhancing
renovations since completion. To obtain one of the units, which are all rental apartments,
young adults must apply at the housing company or at the housing service that allocates
vacant rental apartments in Stockholm. Applicants aged 18–25 years who register interest
and wait the longest will receive a vacant apartment. The rents for these youth apartments
could be considered quite low, especially relative to the costs of the housing
alternatives available to these young adults. Most rental apartments in that same area but
in the ordinary housing stock, i.e., not earmarked apartments, have undergone default-
enhancing renovations with the result that their rents have increased significantly. The
waiting time for such apartments is over 15 years, indicating that this is an attractive
area to which young adults without the possibility of obtaining an earmarked apartment
would normally have difficulties gaining access, unless they can buy an apartment, which
is very expensive. A one room rental apartment in the ordinary housing stock is also on
average 10 square metres larger than the apartments in this Youth House.

<hs>  Data and sample</hs>
  ~~~~~~~~~~~~~~~

The dataset is extracted from a database provided by Statistics Sweden. This database
contains information on all individuals who have resided in Sweden, including their
demographic and socioeconomic situation as well as geocoded data with coordinates and
neighbourhood area codes for where the individuals live. Using this database, it is
possible to link records between individuals and generations, because the data include a
household identity code and, for every individual born after 1932, a specific identity
code for the individual’s mother and father. The sample used in this study consists of
young adults aged 18–25 years who moved into the property earmarked for young adults
(“Youth House”) in Stockholm in 1996. These individuals were defined by identifying the
geographic coordinates of the property, which is located near a large hospital and is
surrounded by a green area. No other residential properties are located immediately
adjacent to the Youth House. Since we in our data also have the geographical coordinates
for everyone, we have been able to define the young adults living a maximum of 30 m from
the property geographical coordinates in 1996, i.e., those 112 young adults aged 18–25
years who moved into Youth House in 1996. This group of young adults will constitute the
treatment group of this study. We will follow them in our data until they have a first
child, complete their higher education, or fourteen years have elapsed (i.e., until 2010).
Their childbearing and education patterns will be compared to those of a matched group of
young adults, i.e., a comparison group of young adults similar to members of the treatment
group in several respects but who did not move into youth housing. The matching procedure
for defining the comparison group of young adults is explained in the next section.

<hs>  Propensity score and matching</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We are in this paper interested in comparing the long-term pattern of childbearing and
education for young adults that entered their housing market through small cheap youth
housing with those who did not and instead received a rental apartment from the ordinary
housing stock. However, those individuals that choose to live in small cheap youth housing
may differ from those that prefer other rental apartments in terms of different attitudes
towards education and family formation, for example. A simple comparison of their
education and childbearing pattern would then be biased by these confounding variables.
This confounding by indication is almost invariably present in non-randomised studies.
Rosenbaum and Rubin (1983) proposed the use of propensity scores as a method for allowing
for confounding by indication. Propensity may be defined as an individual’s probability of
being treated with the intervention of, in this case, entering the housing market through
youth housing, given the information available about that individual. The propensity score
provides a single metric that summarises all the information from the explanatory
variables. Individual subjects may have the same or similar propensity scores, yet some
will start their housing career in youth housing and others will not. An assumption of
propensity score analysis is that a fair comparison of treatment outcomes can be made
between subjects with similar propensity scores who either did or did not start their
housing career in youth housing. The propensity score may be estimated for each subject
from parametric regression in which the treatment is the dependent variable. A feature of
this approach is that explanatory variables are selected based on their ability to predict
exposure to the intervention of interest. Matching is a popular approach employed to
include propensity scores in the analysis, and empirical examples can be found in very
diverse fields of study. Matching requires that each treated individual is matched with
one or several individuals having the same or similar propensity score. By contrasting the
outcomes between treated and untreated sets of individuals with similar propensity for
treatment, we can estimate the average treatment effect.

     <hss>Strategy used</hss>

        To create a balanced (see, e.g., Rosenbaum and Rubin 1983) comparison group of
        young adults in this study, we use the following strategy. First, we identify
        where the individuals who moved into the Youth House in 1996 grow up, i.e. we
        identify the geographical coordinates for the individuals’ parental homes five
        years before they moved into the Youth House, i.e. in 1991. We then identify all
        young adults under 25 years old, with no children and with no higher education,
        who lives within 100 m of each individual in the treatment group in 1991. The
        propensity scores, i.e. the probability of entering the housing market through
        Youth housing, are estimated for all these youngsters as well as for the treated.
        The propensity score has been estimated using a Probit model in which the
        dependent variable is the probability of moving in to the Youth House in 1996.2
        The covariates included in the model are sex, age, and final primary school grade
        as well as family income, parental homeownership status, and whether the parents
        live in single- or multifamily housing. All covariates refer to the situation in
        year 1991, five years before the Youth House was defined. After having estimated
        the propensity scores for all youngsters, we perform a 10 nearest-neighbor
        matching to identify those young adults under 25 years old with no children and no
        higher education living close to each individual in the treatment group with a
        similar propensity score and five years before the Youth House was created.
        Nearest-neighbour matching identifies a control case with a propensity score
        closest to that of each treatment case (see, e.g., Gu & Rosenbaum, 1993). Here, we
        match with replacement, meaning that after a control case is used as a match, it
        is put back into the sample, and can be used again to match other treated units as
        well. After this matching procedure, we have tested whether the treated and
        control groups are balanced with respect to the observed characteristics. The
        result is presented in Table 1. Table 1 show the means of the variables for the
        treatment and matched control groups and our balancing test of the explanatory
        variables cannot reject equality of means between the treated and the matched
        comparisons; the t-values indicate no significant differences between these
        groups, indicating the presence of assessed balance. With 112 individuals in the
        treatment group and 985 in the comparison group, 170 of the comparisons appear
        more than once in the matched data. For a sample to be considered sufficiently
        balanced, Rubin (2001) recommends that Rubin’s B, i.e., the absolute standardized
        difference of the mean linear index, of the propensity score between the treated
        and (matched) control groups, be less than 25 and that Rubin’s R, i.e., the ratio
        of the variance of the propensity score index, between the treated and (matched)
        comparison groups, be 0.5–2.0. Both those recommendations are fulfilled, so the
        matching procedure is deemed satisfactory.

<hs>  Empirical strategy</hs>
  ~~~~~~~~~~~~~~~~~~

We will also include variables indicating when an individual moved from Youth House and to
which tenure type he or she moved, i.e., other rental apartment, cooperative apartment, or
owned housing. 78 percent of the individuals in the treatment group moved from the Youth
House during the observation period. About 40 percent of those moved to cooperative or
owned housing. Note that, after matching a sample, one can simply use the difference
between the treatment and control groups to estimate the average treatment effect.
However, even if we have a matched comparison group, we still want to check whether other
variables not included in the matching procedure may, over time, affect the childbearing
decision or the decision to become educated, differently between the treated and the
compared subjects. These variables are welfare benefits, income from work, and income from
capital. However, including these covariates did not alter the result for the treatment
variable or the conclusions of this study. Young adults who remain childless or do not
complete higher education are censored at the end of the observation period, i.e., in
2010. When modelling a Cox proportional hazard model, a key assumption is the proportional
hazards. Accordingly, we will perform some diagnostic tests for non-proportionality and
estimate parametric models, i.e., the exponential and Weibull models.

<hs>  Becoming parent</hs>
  ~~~~~~~~~~~~~~~

Here we report the results of the Cox proportional hazard models. The tables present the
hazard rates rather than the coefficients themselves. A hazard rate above 1 indicates
increased risk and a hazard rate less than 1 decreased risk. The variable of main interest
in all tables is Youth House, a dummy variable indicating whether the individual moved
into Youth House in 1996, i.e., whether the individual belongs to the treatment group.
Other variables of interest are, as earlier mentioned, a dummy variable indicating the
time point when an individual first moved from Youth House (i.e., Youth House_moved) as
well as dummy variables indicating the type of tenure to which the individual first moved
(i.e., Youth House_moved to rental = moved to another rental apartment, Youth House_moved
to coop = moved to a cooperative, and Youth House_moved to own = moved to owned housing).
Table 2 presents the results of the model with becoming parent as the outcome variable.
Models 1 and 2 present the model results including a variable indicating the time the
individuals move from Youth House. The results indicate that living in Youth House has a
large significant and negative effect on childbearing comparing to those that instead
moved into the ordinary housing stock, a result that is stable even when including
covariates in the model. The hazard of becoming parent while in Youth House is 0.12.
However, moving from Youth House greatly increases the hazard (a hazard of about 17) of
becoming a parent, indicating the importance of a mobile housing market. This result
remains when controlling for the type of tenure to which subjects move when they leave the
Youth House (Models 3 and 4). The hazard of becoming parent are, as expected, largest for
ownership. However, it is also surprisingly higher for those that move to cooperative
apartments than for those that move into a rental apartment in the ordinary housing stock,
a hazard of about 26 compared to 15 for rentals. The results are stable though the sample
is quite small and even when including covariates in the models.

<hs>  Higher education</hs>
  ~~~~~~~~~~~~~~~~

Table 3 presents the results of the education model, i.e., the outcome of completing
higher education. Here, unlike in the childbearing case, we observe a significantly
increased risk of completing higher education for the treatment group, i.e., a positive
effect of Youth House on higher education, corresponding to a hazard of approximately 2.6.
However, the variable indicating a move from Youth House was not significant in this case,
indicating that a mobile housing market seems unimportant to the promotion of higher
education. This result remains when controlling for the type of tenure to which subjects
move (not presented here). None of those variables were significant.

<hs>  Sensitivity tests</hs>
  ~~~~~~~~~~~~~~~~~

All the models were also estimated using the exponential and Weibull models. The Weibull
model is more general and flexible than is the exponential model and allows for hazard
rates that are non-constant but monotonic. The results of both these models were in line
with those of the Cox model presented in Sections 4.1 and 4.2. As already mentioned, a key
assumption when testing such models concerns the proportional hazards. We accordingly
performed the Schoenfeld residuals test, developed by Therneau and Grambsch (2000), to
test the proportional hazard assumption. We found no evidence that the models with higher
education as the outcome violated the proportional hazard assumption, nor that the models
with the outcome childbearing that did not include the variable indicating a move from
Youth House violated the same assumption. For the other models, the results of the
Schoenfeld residual test indicated non-proportional hazards. One solution to this
potential problem is to interact the variables displaying signs of non-proportional
hazards with the natural log of time (Box-Steffensmeier & Zorn, 2001, p. 978) to
explicitly allow the effect of the variable to vary across time. We did this for all
variables that displayed signs of non-proportional hazards; this, however, did not alter
the results. All the variables of interest were still highly significant, with the same
estimate size as with the Cox model.

<h>CONCLUSIONS AND POLICY IMPLICATIONS</h>
-----------------------------------

The point of departure of this study was to examine the effect of youth dwellings, i.e.,
apartments earmarked for young adults, on young adults’ childbearing and education
patterns. Youth dwellings are often small and lack proper kitchen facilities, and
therefore do not necessarily facilitate family formation. If access to higher-quality
housing is difficult because of scarcity, high prices, and strict mortgage provision,
young people might postpone childbearing if housing of a certain standard is desirable
when forming a family. However, young adults who leave the parental home for education may
have little latitude for postponement and may therefore obtain an education despite living
in substandard housing. We have in this paper compared the long-term pattern of
childbearing and education for young adults that entered their housing market through
small cheap youth housing with those youngsters that received a rental apartment from the
ordinary housing stock. To be able to draw the conclusion that differences in fertility
and educational pattern between these two groups comes from the different housing
situation and not from differences in preferences when it comes to childbearing or
individual prerequisites for higher education, we have used a geocoded data and
information on the individual’s family background as well as a matching technique to
create a comparison group. An assumption of propensity score analysis is that a fair
comparison of treatment outcomes can then be made between subjects with similar propensity
scores who either did or did not start their housing career in youth housing. The present
results indicate that gaining access to a small, low-rent inner-city apartment earmarked
for young adults may promote higher education but negatively affect childbearing unless
the rest of the housing market is mobile, i.e., enables young adults to advance in their
housing careers. However, the effect of such housing on higher education is independent of
mobility in the rest of the housing market. So, what are the policy implications of our
finding? The key policy implications of these results are that: Building affordable
housing that is small and space efficient is sufficient and positive if the aim is to
promote higher education. Affordable housing is on the other hand not enough to promote
childbearing, instead, it seems to inhibit childbearing until there is a possibility of
moving on in the housing career. Our result indicates also that the next step need not
necessarily be homeownership, as earlier research has indicated. Entering the housing
market via youth housing and then being able to move on to rental accommodation in the
ordinary housing market also seems to have a positive effect on overall childbearing,
although moving to cooperative housing or owned housing has an even larger effect. These
results may lead to a deeper understanding how policy makers may promote childbearing and
higher education through the housing market, something that seems to be a necessity to
attract and retain younger residents. Small apartments for younger people in an area where
most elderly or families with children live may also create a good dynamic and a variety
of people. It also creates a broader service and store range and a good basis for public
transport. However, the present results do not allow us to determine the driving force of
the results achieved by youth housing. Is it that young adults do not find the general
concept of youth housing compatible with childbearing, or is it that the dwellings are
small and lack proper kitchen facilities, i.e., the housing size and standard do not meet
the quality norms required for childbearing? Or does the relatively low rent make
alternative accommodations seem too expensive, creating a lock-in effect that postpones
childbearing? Answering these questions requires more data and further research into youth
housing.


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----------

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<ART>The role of consumer networks in firms’ multi-characteristics competition and market share inequality
================================================================================

Authors: Antonios Garas, Athanasios Lapatinas
DOI: 10.1016/j.strueco.2017.08.004
Year: 2017  |  Pages: 76-86
ASJC codes: 2002
Keywords: Agent-based model, Decision heuristics, Location choice, Multi-characteristics space, Networks, Political competition, consumer behavior

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

We develop a location analysis spatial model of firms’ competition in multi-characteristics space, where consumers’ opinions about the firms’ products are distributed on multilayered networks. Firms do not compete on price but only on location upon the products’ multi-characteristics space, and they aim to attract the maximum number of consumers. Boundedly rational consumers have distinct ideal points/tastes over the possible available firm locations but, crucially, they are affected by the opinions of their neighbors. Proposing a dynamic agent-based analysis on firms’ location choice we characterize multi-dimensional product differentiation competition as adaptive learning by firms’ managers and we argue that such a complex systems approach advances the analysis in alternative ways, beyond game-theoretic calculations.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Product characteristics are typically considered as given when economists study firms’
strategies and behaviour. But firms in industries with product differentiation actually
choose the features of their products based on consumers’ preferences. The role and
effects of the demand side in product differentiation processes have been neglected by the
relevant literature (Coombs et al., 2001; Mueller et al., 2015) and only recently have
started to receive attention (Andersen et al., 2011). The importance of consumer behaviour
in shaping markets’ properties is oversighted and in most cases the simplistic perspective
of perfect rational homogeneous agents is implicitly adopted in the literature (Valente,
2012). Among the works highlighting the relevance of demand for the emergence of new
products, Witt (2001), Saviotti (2001), Malerba et al. (2007), Windrum et al. (2009),
Nelson and Consoli (2010), Valente (2012), Markey-Towler and Foster (2013), Mueller et al.
(2015), Markey-Towler (2016) and Schlaile et al. (2017) can be included. However, no
attention has been paid to advancing a generalized evolutionary model of demand for the
effect of consumers’ social networks on their consumption decisions and, in turn, on
firms’ process of developing new characteristics for their products. The aim of this paper
is to address this gap in the literature by suggesting a way to understand the relevance
of consumers’ social networks in shaping demand behaviour in such markets, which in turn
frame the process of product-embodied innovations. We do so using complex networks, which
mathematically are described by graph objects. We develop a stylized computational model
to examine the issue of product differentiation in a multi-dimensional space with
consumers’ choices emerging from consumers’ opinion-based multilayered networks. The model
that we propose is designed to analyze and illustrate potential effects of consumers’
heterogeneity, particularly regarding their preferences, their bounded rationality and the
role of their social networks on the development of new product characteristics. We ask
two questions: First, how consumers’ social networks affect their decisions on which
products to buy and how this decision leads to market-share inequality at the firm level?
Second, how firms respond to these decisions by developing new characteristics for their
products defined over a multidimensional characteristic space? Assuming that bounded
rational consumers with heterogeneous preferences can have an active role in the product-
embodied innovation process, and studying the influence of a change in their purchasing
opinion over time due to their participation on social networks calls for new modelling
approaches, namely complex systems analysis and agent-based simulation techniques (Pyka
and Grebel, 2006; Pyka and Fagiolo, 2007; Gilbert, 2008; Farmer and Foley, 2009; Tubaro,
2011; Schlaile et al., 2017; Muller, 2017). Agent-based simulation approaches focus on the
rules and elements that constitute a system and the interactions of the players/agents
within the system and have gained increasing momentum in many scientific disciplines
(Schlaile et al., 2017; Mueller and Pyka, 2017; Vermeulen and Pyka, 2016; Namatame and
Chen, 2016; Hamill and Gilbert, 2016; Boero et al., 2015; Wilensky and Rand, 2015; de
Marchi and Page, 2014; Kiesling et al., 2012). In our case, through agent-based simulation
we are able to account for the economic agents’ heterogeneity and the related implications
of their interactions by representing the economic system in a more realistic fashion
overcoming the simplistic models limited to representative agents (Bonabeau, 2002; Macal
and North, 2005, 2006, 2010, 2014; Page, 2011; Schalaile et al., 2017). The agent-based
simulation model described in this paper is based on the works by Laver, (2005), Laver and
Sergenti (2011), Valente (2012), Markey-Towler and Foster (2013), Halu et al. (2013),
Mueller et al. (2015), Schlaile et al. (2017), Muller (2017) and represents a first
attempt to address the issue of neglected consumers’ social networks in the process of
developing new products. In particular, we focus on the effects of heterogeneous and
boundedly rational consumers’ social networks on firms’ multi-dimensional product
differentiation competition.1 Our model captures only parts of the consumers’ demand-side,
namely ‘consumption as voting’ (Dickinson and Carsky, 2005; Shaw et al., 2006; Moraes et
al., 2011) whereby consumers choose which firms/suppliers and new products/services to
support.2 In this sense, our model could also apply to political competition, as studied
by Downs (1957) and many others after him. More specifically, it could be perfectly placed
within the scope of agent-based models described in Laver and Sergenti (2011). However, in
this work we will stick to the firm affairs’ language. In more detail, what we propose
here is a multi-dimensional agent-based model of firms’ locational choice in the product-
characteristics space that describes a finite number of firms competing for customers.3
This model is inspired by the New Consumer Theory literature dealing with the non-price
aspects of consumer behaviour (Lancaster, 1966, 1971, 1975, 1979; Ironmonger, 1972;
Ratchford, 1975; Earl, 1983, 1986) and has its roots in the behavioral economics
literature having to do with boundedly rational consumers making decisions under the
presence of multiple attributes (Selten, 1998). From consumers’ perspective, we begin with
a very basic idea. Consumers’ decision on purchases cannot be different from most other
decisions people make in their daily lives, in the sense that some process for acquiring
information and evaluating it is necessary. The model also allows for heterogeneity of
demand based on heterogeneous consumers having individual preferences for the particular
characteristics of the products, like the colour, the size, the brand, the shape, their
functionality etc.: consumers have preferences that place them on their ideal points in a
multi-characteristics space.4 For every firm we model the network of consumers’ opinions
about its product (i.e. for every firm there is a corresponding opinion network describing
consumers’ opinion about the firm’s product: the nodes represent the consumers and a link
between two nodes represents their exchange of opinion about the corresponding firm’s
product), on which (opinion network) a contagion dynamics can take place.5 Consumers are
represented on every network and can be active only in one of the networks (purchase of
one product from one firm) at the end of a given time period (at the moment of the
purchase). Each consumer has also the option not to purchase, and in that case she will be
inactive in all networks. Before the end of each time period, and while the consumers
think about the purchase, they are more likely to change opinions and examine different
options. They have some form of product characteristics expectations at the beginning,
which is reflected by their position in the product characteristics space, but their
decision on which product to purchase is crucially affected by the opinion of their peers:
at the time of the purchase, they tend to be active in the network where the majority of
their peers are also active.6 In addition, as they gain experience and acquire more
information about the products, their opinion can change, but it stabilizes over time (see
Hoeffler and Ariely, 1999; West et al., 1996). This “uncertainty reduction”, reflecting
both consumers’ learning and changes in their environment, is captured by dynamics that
slow down until the purchase moment when they become completely frozen. These dynamics are
implemented in this work with the simulated annealing algorithm.7 An illustration of a
possible final configuration of the described system is shown in Fig. 1. At the end of the
simulated annealing calculation we have the number of consumers that opt to purchase from
each firm. This is affected by the average connectivities of the consumers’ opinion
networks. Hence, we observe “regions” in the average connectivity space where the active
nodes belonging to some opinion networks with high average connectivity percolate the
system, while nodes of the remaining opinion networks with lower average connectivities
are concentrated in disconnected clusters indicating high market share inequality.
Nevertheless, “regions” where the average connectivities of the consumers’ opinion
networks are comparable manifest a market that sustains low market share inequality (see
also Halu et al., 2013). To the best of our knowledge, this paper is the first study that
incorporates the role of opinion exchange and processing on a multilayered network, in an
attempt to shed light on how the market-share inequality and the competition in a multi-
characteristics space are affected by the presence of consumers’ interactions.8 Taking
into account these multiple layers is crucial, as the considerable interest in various
multilayered systems demonstrates (Buldyrev et al., 2010; Vespignani, 2010; Parshani et
al., 2011; Baxter et al., 2012; Bashan et al., 2012; Gomez et al., 2013; Radicchi and
Arenas, 2013; De Domenico et al., 2013; Radicchi, 2014; Garas, 2016). On the other hand,
to make significant advances in understanding consumers’ decisions, we must device a
method for studying this process. Such method would allow us to observe consumers’
behaviour from up close, to dig below the surface and watch consumers as they try to
exchange information about a myriad of alternative products while refining the
overwhelmingly volume of information of their multiple characteristics. Behavioral
decision theory guides the process-oriented, complex systems-framework we present in the
next sections in an effort to develop a new set of measures for studying market
proceedings. The results reported in the subsequent sections are intended to demonstrate
that such a realistic complex systems approach provides a plausible basis for
understanding market-share inequality and firms’ competition in the product-
characteristics space and can advance the analysis of these topics in interesting and
alternative ways, beyond game-theoretic calculations. The rest of the paper is organized
as follows. In Section 2 the agent-based model (ABM) is introduced, section 3 gives the
simulation strategy and discusses the simulation results and Section 4 concludes.

<hs>  Consumers’ behaviour</hs>
  ~~~~~~~~~~~~~~~~~~~~

Traditionally the assumed heuristic for consumers is a maximization rule over some utility
function defined over the set of products’ quantities. However, this rule is inconsistent
with extensive evidence presented in behavioral economics and marketing literature. Here
we assume that each consumer’s preferences can be characterized by an ideal economic
position in some k-dimensional product characteristics space, and we look closely on the
decisions made by consumers when choosing which firm’s product to buy. Having switched
from formal analysis to computation, we depart from the classical analytically tractable
models first, by assuming as baseline decision rule that consumers are affected by the
opinion of their peers and second, by making the appropriate behavioral assumptions
following the relevant literature of behavioral economics, discussed below. Behavioral
decision theory is psychological in its orientation, beginning with the view of humans as
limited information processors or, perhaps more accurately, as “boundedly rational
information processors” (Simon, 1955, 1956, 1957, 1959). Humans have developed a large
number of cognitive mechanisms to cope with the overwhelming volume of information in the
modern societies. These mechanisms are adopted automatically without any conscious and are
cognitive shortcuts for making certain judgments and inferences with considerably less
alternatives than those dictated by rational choice, focusing attention on a small subset
of all possible information. Kahneman and Tversky (1973, 1974, 1984) and Tversky and
Kahneman (1973, 1974) have identified three general cognitive heuristics that decision
makers adopt in the process of information gathering and analysis: (a) decomposition,
which refers to braking a decision down into its component parts, each of which is
presumably easier to evaluate than the entire decision; (b) editing or pruning, which
refers to simplifying a decision by eliminating (ignoring) otherwise relevant aspects of
the decision; (c) decision heuristics, which are simplifying the choice between
alternatives thus providing cognitive efficiency. These heuristics have direct application
to consumers’ choices. Consumers face a myriad of alternative products and there is
compelling evidence which suggest that consumers simplify their decisions with a consider-
then choose decision process in which they first identify a set of products, the
consideration set, for further evaluation and then choose from the consideration set. In
seminal observational research Payne (1976) identified that consumers use consider-then-
choose decision processes. This heuristic is firmly rooted in both the experimental and
prescriptive marketing literature (e.g. Bronnenberg and Vanhonacker, 1996; Brown and
Wildt, 1992; DeSarbo et al., 1996; Hauser and Wernerfelt, 1990; Jedidi et al., 1996; Mehta
et al., 2003; Montgomery and Svenson, 1976; Paulssen and Bagozzi, 2005; Roberts and
Lattin, 1991; Shocker et al., 1991; Wu and Rangaswamy, 2003).

<hs>  Evolution dynamics during consumers’ purchasing process</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Initially, active nodes in each network j are distributed according to consumers’
consideration sets [Eq. (3)], and we allow the consumers to change opinion at any time
before they make their final choice. These dynamics are implemented using the simulated
annealing algorithm, which works as follows. Starting from a relatively high initial
temperature, T,11 i.e. a large number of potential conflicts [a large-number of non-
binding constraints given by Eq. (4), hence a high H given by Eq. (5), which means that
before the purchase time, consumers can be active in more than one network, i.e. they can
have positive opinion for more than one firm/product] due to the stochastic way initial
opinions are distributed, we use a Monte Carlo dynamics which will reach an equilibrium
following the equation (5). As the time for the final choice approaches, i.e. as the
simulated annealing progresses, the effective temperature T decreases and the consumers
tend to have less and less opinion conflicts with their network peers until they reach to
zero conflicts at equilibrium, when H = 0.

<hs>  Firms’ ‘behaviour’</hs>
  ~~~~~~~~~~~~~~~~~~

Following Laver and Sergenti (2011) we assume that firms’ managers use an adaptive
decision rule to set product characteristics on a multidimensional product-characteristics
space at any given period t. We assume an adaptive rule that models a manager who
constantly modifies product characteristics in the search for more customers, and the
manager cares only about the firm’s market share. If the manager’s decision for the
characteristics of the product at time t was rewarded by an increase in market share, then
the firm makes a unit move at time t + 1 in the same direction as the move at t. If not,
the manager reverses direction and makes a unit move on a heading randomly selected within
the half-space being faced now. In other words, the firm’s manager relentlessly forages in
the product-characteristics space, always searching for more customers and never being
satisfied, changing strategic planning in the same direction as long as this is rewarded
with more sales, but casting around for a new strategic planning when the previous one was
punished with falling or static sales. Now that we have structurally defined the evolution
process of the complex system as a whole, we can proceed to simulations.

<h>SIMULATIONS</h>
-----------

For clarity in what follows we consider two firms, hence two layers in the consumers’
opinion network, in the simulation experiments. Though, our code can be straightforwardly
generalized to consider multiple firms/networks. In our setting, consumers are assumed to
be intrinsically interested in product characteristics and to have ideal points in a
product-characteristics space (again, in order to aid visualization, the simulated version
of the model is implemented in two dimensions, i.e. in the Euclidean plane, but the model
can be implemented in any number of dimensions). Firms compete with each other by offering
products with varied characteristics to consumers. Fig. 2 summarizes the model and its
evolution process, which was programmed in R.

<hs>  Firm system dynamics</hs>
  ~~~~~~~~~~~~~~~~~~~~

Initiation of the model randomly distributes a discrete set of firms’ locations and
consumers’ ideal points across the product-characteristics plane.13 Consumers are
initially present and active in the opinion-networks/firms which lie within their
consideration sets. As discussed above (see Section 2.3), we allow the consumers to change
opinion at any time before they make their final choice, and we model their dynamics using
the simulated annealing aiming to reduce to zero the number of conflicts with their
network peers (the number of violated mathematical constraints given by Eq. (4) for all
consumers) when reaching equilibrium. More precisely, following Halu et al. (2013), the
algorithm starts with an initial temperature T = 1 and at every time step we select a node
at random from either one of the two networks with equal probability and we change it from
active to inactive or vice versa. After this change, the Eq. (5) is recalculated, and if
the difference with respect to its previous value, ΔH, is negative i.e., the number of
conflicts in the system is reduced, the change is accepted. If ΔH > 0, the change can
still be accepted but with a small probability given by e−ΔΗ/kT. This random selection
process is repeated 2N time steps, in order to update the whole system on average once and
then we advance the system time by one Monte Carlo step. The whole process is repeated by
slowly reducing the temperature until we reach equilibrium at H = 0, where there are no
more conflicts in the network. The final configuration of the “uncertainty reduction”
process just described is depicted in Fig. 1. The simulation results visualized in Fig. 3
are in accordance with the findings of Halu et al. (2013) and imply that the firm with the
most connected customers gets the lion’s share of the market: Case 1: In the regions where
the mean degree of both networks is smaller than one, there are no giant components in the
networks. This means that the networks are fragmented and the opinion of a consumer is not
affected by peer opinions. In this case each firm possesses only a marginal market share
and noticeable market share inequality is unlikely. Case 2: In the regions where the mean
degree of either one of the two networks is smaller than one and for the other network
bigger than one, the giant component in the latter network emerges and market share
inequality occurs. Case 3: In the regions where the mean degree of both networks is
greater than one, giant components emerge in both networks. In these regions we have the
pluralism solution of the consumers’ choices and hence, no noticeable market share
inequality is apparent. Once consumers have purchased products, firms’ managers adapt
their locations to reflect the pattern of consumers’ preferences. Firms’ managers are
assumed to use an “unconstrained” adaptive rule that constantly modifies product
characteristics in the search for more customers. The rule searches for customers using a
“win-stay, lose-shift” algorithm (Nowak and Sigmund,1993; Bendor et al., 2003; Laver,
2005): if the previous move increased market share the manager makes another unit move in
the same direction. If the previous move did not increase market share, the manager makes
a unit random move in the opposite direction chosen randomly within the half space toward
which it now faces.15 Managers use no information whatsoever about the global geography of
the product-characteristics plane. They have no knowledge of the ideal point of any
consumer but applying recursively the limited feedback from their local environment they
pick up effective clues about the best direction in which to move. Once firms’ managers
have adapted firms’ positions, consumers readapt and once more are active in the opinion-
networks/firms which lie inside their consideration sets. Then they are again affected by
peers’ opinions till their final decision on which product to purchase, then firms readapt
to the new configuration of consumers’ preferences and the process iterates continuously.

<hs>  Location choice</hs>
  ~~~~~~~~~~~~~~~

In the previous section we analyzed consumers’ behaviour when their opinions are affected
by the opinions of their network peers and the effect of this process in firms’ market
share. Next, we consider firms’ location choice on the product-characteristics plane with
origin (0,0) assuming that consumer ideal points’ distribution is normal on both product-
characteristics’ dimensions.16 We check whether certain product differentiation patterns
emerge. Summarizing, Fig. 4 discloses the following scenarios for the different phases of
the model: Scenario I:〈k〉A ≫ 〈k〉B. In this case, firm B moves toward the center of the
product-characteristics plane searching for customers while the firm A with better
connected consumers can afford to roam anywhere in the product characteristics plane.
Scenario II:〈k〉A ≈ 〈k〉B. In this case, no firm has a significant advantage over its
competitor due to the presence of the opinion-network. Therefore, very much along the
lines predicted by the traditional spatial competition model, both firms systematically
move toward the center of the product-characteristics plane. Scenario III:〈k〉A ≪ 〈k〉B. In
this case, it is firm B that can afford to roam anywhere in the product-characteristics
plane when the firm A with the poorly connected underlying opinion-network is hunting
customers moving towards the highest density of consumers.

<h>CONCLUSIONS</h>
-----------

This paper contributes to the literature of product-characteristics competition at the
firm-level by proposing an evolutionary economic approach that focuses on the role of
consumers’ social networks in the creation of new product characteristics. In the
evolutionary framework, firms’ competition for market share depends on the
preferences/tastes of many economic agents that interact and exchange
knowledge/ideas/opinions, thereby forming complex social networks which condition the
evolution of the process. The influence of consumers’ social networks in the development
of new products is neglected in the traditional literature with ‘passive’ and homogeneous
consumers: consumption is aggregated into economy’s demand side and it is reduced to the
purchase decision only, excluding social interactions. On the supply side, firms’ managers
incorporate new characteristics to their products that consumers can either buy or not
without taking into account consumers’ heterogeneous preferences and the role of their
social networks. Filling this gap, we put forth a product-characteristics competition
spatial computational model based on complex systems science. Moving away from the
forward-thinking strategic game theoretic models, we argue that consumers’ boundedly
rational behaviour within their opinion exchange networks can result in concentrated power
nodes in the network structure of the market. We confirm Halu et al. (2013)’s finding that
the key feature to get the higher share of the overall product-purchases is the
connectivity of the consumers’ opinion networks corresponding to different firms.
Regarding firms’ location, we use agent-based modeling to study multi-characteristics
competition in the evolving market. We are interested in location competition among
multiple firms in a multidimensional product-characteristics environment in which
consumers and firms care for more than one product characteristic. We show that for the
case of strong inequality in the density of firms’ underlying opinion-networks, the firm
with the highly connected network is roaming anywhere in the product-characteristics plane
away from its origin, despite the fact that this is the location of the highest density of
consumers. The opposite is true, with the firms approaching the center more often, when
their underlying networks are weak or when all underlying networks are strong and no firm
has a relative advantage on this. Most of the relevant literature considers consumers’
preferences as exogenous, referring to behavioral heuristics as determinants that lie
outside the sphere of economics (Bowles, 1998). Valente (2012) argues that this assumption
is used as a justification for aggregating towards a representative consumer and avoiding
the economic analysis of heterogeneous agents with different preferences. Experimental and
cognitive psychology empirical evidence shows that preferences are not exogenous but
rather seem to be constructed during their elicitation (Shafir et al., 1993) and,
furthermore, are influenced by the preferences of other agents (Tversky and Kahneman,
1981; Kahneman et al., 1982). This means that an interested party, like a firm competing
for customers, might be able to shape consumers’ decisions towards a specific option by
influencing their preferences or affecting the opinions of their peers. Besides, it is
well known that a very large share of companies’ expenditures is devoted to marketing
usually designed to press consumers to adopt a particular perspective/opinion of the
product. In this paper, we demonstrate how consumers’ social networks can be considered
the link between the supply side of the market (managers’ decision on marketing and
strategic directions) and the demand side (consumers’ preferences influenced by managers’
strategies). In this way, we capture the feedback loop between consumers and firms, namely
consumers’ preferences guiding firms’ innovation strategies and on the other way around,
firms shaping consumers’ preferences by pursuing the consolidation of dense underlying
social networks. The consumers’ social networks are appealing to organizations not only as
a low cost way of reaching an audience, but also for their increasing penetration into
everyday life and decision making due to the acceleration of the social media in the web
(Sadovykh et al., 2015). Our paper is also related to the recent works by Vitell (2003),
Vitell (2015), Schlaile et al. (2016), Schlaile et al. (2017), Muller (2017) on the role
of consumers in responsible innovation and demand. This strand of literature illustrates
that consumers’ heterogeneity and bounded rationality plays an important role in the
creation and diffusion of responsible innovations. The results suggest that when all
consumers focus solely on negative characteristics and demand only “responsible” products
and services then the complex interplay between demand and supply can create situations
that are inferior to scenarios with fewer responsible consumers. Along these lines, our
model could easily be expanded to include negative product characteristics allowing the
identification of central actors that have the power of influencing their peers’ opinions
towards consuming more responsibly. Our complex networks approach may also be appropriate
to address the issue of public and stakeholder engagement for stimulating responsible
innovation (Jackson et al., 2005; Chilvers, 2008; Delgado et al., 2011; Owen and Goldberg,
2010; Blok et al., 2015). Though we miss the analytical tractability of the relevant
theoretical models, our simulated results demonstrate the feasibility of agent-based
techniques to describe and explore firms’ locational choices, as well as the capability of
the proposed model to further advance the analysis in alternative ways beyond the game-
theoretic framework. The proposed model should be seen only as a starting point for
further research on the role of consumers in shaping markets since the real world is far
more complex than our model with various aspects and factors influencing consumers’
decision making. One interesting direction for future research might be the extension of
our model towards considering the role of committed agents i.e. the situation in which a
fraction of consumers always remains active in one of the networks, never changing its
opinion (Galam and Moscovici, 1991; Galam and Jacobs, 2007; Xie et al., 2011; Mobilia et
al., 2007; Halu et al., 2013; Masuda, 2015). Likewise, it might be also interesting to see
whether the assumption of some “iconoclast consumers”, i.e. consumers who intentionally
behave opposite to the tendencies of their peers, alters our results.


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<ART>The role of nutrition and genetics as key determinants of the positive height trend
================================================================================

Authors: P. Grasgruber, J. Cacek, T. Kalina, M. Sebera
DOI: 10.1016/j.ehb.2014.07.002
Year: 2014  |  Pages: 81-100
ASJC codes: 2001
Keywords: Europe, GDP per capita, Genetics, Male height, Nutrition

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

The aim of this study was to identify the most important variables determining current differences in physical stature in Europe and some of its overseas offshoots such as Australia, New Zealand and USA. We collected data on the height of young men from 45 countries and compared them with long-term averages of food consumption from the FAOSTAT database, various development indicators compiled by the World Bank and the CIA World Factbook, and frequencies of several genetic markers. Our analysis demonstrates that the most important factor explaining current differences in stature among nations of European origin is the level of nutrition, especially the ratio between the intake of high-quality proteins from milk products, pork meat and fish, and low-quality proteins from wheat. Possible genetic factors such as the distribution of Y haplogroup I-M170, combined frequencies of Y haplogroups I-M170 and R1b-U106, or the phenotypic distribution of lactose tolerance emerge as comparably important, but the available data are more limited. Moderately significant positive correlations were also found with GDP per capita, health expenditure and partly with the level of urbanization that influences male stature in Western Europe. In contrast, male height correlated inversely with children's mortality and social inequality (Gini index). These results could inspire social and nutritional guidelines that would lead to the optimization of physical growth in children and maximization of the genetic potential, both at the individual and national level.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

The increase of height in the industrialized world started only ∼150 years ago. In the
past, adult stature reflected fluctuations in environmental factors influencing physical
growth (mainly climate, diseases, availability of food and population density) and
considering that these conditions have almost never been optimal, it is not surprising
that height could not approach maximal genetic limits. Paradoxically, the tallest people
in Europe before the start of the industrial revolution may have been Early Upper
Paleolithic hunters from the Gravettian culture that emerged at least ∼36,000 calibrated
years ago (Prat, 2011) and is connected with the migration from the Near East that brought
Y haplogroup (male genetic lineage) I-M170 to Europe (Semino et al., 2000). The estimated
stature of Gravettian men is thought to be tall in the whole of Europe: 176.3 cm in
Moravian localities (n = 18) and 182.7 cm in the Mediterranean (n = 11) (Dočkalová and
Vančata, 2005). These exceptional physical parameters can be explained by a very low
population density and a diet rich in high quality animal proteins. However, Late Upper
Paleolithic and especially Mesolithic Europeans were noticeably smaller; Formicola and
Giannecchini (1999) estimated that the average height of Mesolithic males was 173.2 cm (n
= 75) in the Carpathian Basin and Eastern Europe, and only 163.1 cm (n = 96) in Western
Europe. Perhaps the lowest values in European history were recorded in males from the Late
Neolithic Lengyel culture (in the Carpathian Basin during the 5th millenium BC), who were
only 162.0 cm tall (n = 33) (Éry, 1998). A new increase (up to ∼169 cm) came during the
3rd millenium BC with the advance of Eneolithic cultures (Corded Ware culture, Bell-Beaker
culture) (Vančata and Charvátová, 2001; Dobisíková et al., 2007) and it is tempting to
speculate that it was just in this period, when beneficial genes of lactose tolerance
spread in Central and Northern Europe, because their origin is placed in the Neolithic era
(Itan et al., 2009). During the next millenia, stature of Europeans changed mostly due to
climatic conditions and usually remained within the range of ∼165–175 cm (Hermanussen,
2003; Steckel, 2004; Koepke and Baten, 2005; Mummert et al., 2011 etc.). The modern
increase of stature in the developed world is closely tied with the positive effect of the
industrial revolution. Ironically, these socioeconomic changes were accompanied by a new
temporary decline of body size in the late 18th century and then again in the 1830s, which
probably resulted from bad living conditions in overcrowded cities, a worsening of the
income distribution and the decline of food available per capita1 (Komlos, 1998; Steckel,
2001; Zehetmeyer, 2011). These negative circumstances were overcome at the end of the 19th
century and since that time the trend of height increase in Europe has been practically
linear (Baten, 2006; Danubio and Sanna, 2008; Baten and Blum, 2012). Before WWII, its pace
was faster in the northern and middle zone of industrialized Europe, while after WWII, it
was mainly countries in Southern Europe that experienced the biggest increments (Hatton
and Bray, 2010). Approximately since the 1980s, a beginning deceleration or even
stagnation started to be apparent in some nations. After being the tallest in the world
for 200 years, the US was overtaken by many Northern and Western European countries such
as Norway, Sweden and the Netherlands (Komlos and Lauderdale, 2007). Various authors tried
to identify the most important environmental variables that contributed to this dramatic
increase of height in the industrialized world. Besides GDP per capita (as the main
indicator of national wealth), the most frequently mentioned factors are children's
mortality, the general quality of health care, education, social equality, urbanization
and nutrition (Komlos and Baur, 2004; Baten, 2006; Bozzoli et al., 2007; Baten and Blum,
2012; Hatton, 2013 etc.). However, the number of investigated European countries is
usually limited to the western half of the continent and to former European colonies,
because information from the rest of Europe is less accessible. In the present work, we
fill this gap. The aim of this study can be summarized in four basic points: Mapping the
current average height of young males in nations of European descent and describing the
actual dynamics of the height trend. Identifying main exogenous (environmental) factors
that determine the final male stature. Creating recommendations that could lead to the
maximization of the genetic potential in this regard. Investigating the role of genetics
in the existing regional differences in male height.

<hs>  Collection of anthropometric data</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

In order to have the most representative basis for our comparisons, we collected a large
number of anthropometric studies of young European males from the whole continent
(including Turkey and the Caucasian republics), and also data on young white males from
Australia, New Zealand and USA. Whenever possible, we preferred large-scale nationwide
surveys that have been conducted within the last 10 years and included at least 100
individuals. Forty-six out of 48 values in Table 1 were based on studies that were
conducted between 2003 and 2013. The remaining two studies (from Australia and Lithuania)
were done between 1999 and 2001. In case we found two or more representative sources from
this period, we preferred those with higher measured values. In general, information from
the southeastern part of Europe was the most problematic, because large-scale, nationwide
anthropometric research is often virtually non-existent. The only country from which we
had data on less than 100 individuals was Georgia (n = 69).2 In seven cases, we found the
most recent data only on local populations (Bosnia and Herzegovina, Georgia, Iceland,
Latvia, Romania, Sweden and United Kingdom). The urban surveys from Iceland and Latvia may
increase the real national mean, but the study from Iceland was undertaken in the greater
area of Reykjavik that encompasses ∼70% of the Icelandic population. The mean for the
United Kingdom (177.7 cm) was computed from the average height in England, Scotland and
Northern Ireland, weighted by the population size. A weighted average of six adult, non-
university samples from Bulgaria was 175.9 cm (n = 643), which agrees with a rounded mean
176 cm (n = 1204) reported in the age category 25–34 years in a recent nationwide health
survey CINDI 2007 (P. Dimitrov–pers. communication). In the case of Romania, we used an
unweighted average of 3 local surveys (176.0 cm). Similarly, the average height in Bosnia
and Herzegovina (182.0 cm) was computed as an unweighted mean of two local studies in the
city of Tuzla, Northeastern Bosnia (178.8 cm), and in Herzegovina (185.2 cm),
respectively. Because of the large (6+ cm) difference between these regions, this estimate
must be considered only as very rough. However, considering that Herzegovinians used to be
the tallest in the country and inhabitants of Tuzla the shortest (Coon, 1939), it appears
reasonable.3 The average of Herzegovina was further corrected by +1 cm for unfinished
growth in 17-year olds, which increased the average of Bosnia and Herzegovina to 182.5 cm.
The addition of +1 cm to the height of 17-year old Ukrainian boys increased the Ukrainian
mean to 176.9 cm.4 In another two countries (Armenia and Moldova), male height was
estimated, based on highly representative data of 20–24 year old women from demographic
and health surveys (DHS): 159.2 cm for Armenia (n = 1066) and 162.3 cm for Moldova (n =
1099). These female means were multiplied by 1.08, which was the average ratio of male and
female height in 36 countries, where data on both sexes were available from the same
study. The obtained values—171.9 cm for Armenia and 175.3 cm for Moldova—appear
reasonable, because male and female height in these 36 studies mutually highly correlated
(r = 0.91; p < 0.001). No information on measured height was available from Luxembourg,
Malta and Wales.

<hs>  Exogenous and genetic variables</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Data from these anthropometric surveys were subsequently used for a geographical
comparison of European nations (Fig. 1) and for a detailed analysis of key factors that
could potentially play a role in the current trends of male height in Europe, primarily
with the help of statistics from the CIA World Factbook (the Gini index), FAOSTAT (food
consumption) and especially the World Bank, which contained all other variables that we
examine (GDP, health expenditure, children's mortality, total fertility, urbanization).5
Since the final adult stature can be influenced by changes in living standards up to the
cessation of growth, it was not surprising that long-term averages of these variables
routinely produced higher correlation coefficients than data from the latest available
year. However, data from all these sources were available only since 2000 and our analysis
was therefore limited to long-term means from the period 2000–2012. The only exception was
the Gini index (which was based on the latest available year from 1997 to 2011) and
nutritional statistics (FAOSTAT 2000–2009), where the mean of Montenegro was computed only
from the period 2006–2009. Genetic profiles of European nations (the phenotypic incidence
of lactose tolerance, Y haplogroup frequencies in the male population) were obtained from
various available sources and the most numerous samples were always preferred. Only
samples with at least 50 individuals were included (see Appendix Tables 3a–d). Frequencies
of Y haplogroups (male genetic lineages) E-M96, G-M201, J-P209, R1a-M420 and I-M170 were
available from 43 countries (with only Australia and New Zealand missing), but the
information on R1b-U106 and R1b-S116 was more limited, because these two lineages were
discovered relatively recently (Myres et al., 2011). Nevertheless, most of the missing
information concerned the eastern and southeastern parts of Europe, where their frequency
is often close to zero and thus largely unimportant for this study. A similar limitation
applied for lactose tolerance, where we found data only from 27 countries.

<hs>  Statistical analyses</hs>
  ~~~~~~~~~~~~~~~~~~~~

The analysis of the data collected was performed by the software package Statistica 12.
Statistical relationships between variables were first investigated via Pearson's linear
correlation coefficients. Subsequently, we identified the most meaningful factors via a
series of stepwise regression analyses.

<hs>  Distribution of average male height in Europe</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The average height of 45 national samples used in our study was 178.3 cm (median 178.5
cm). The average of 42 European countries was 178.3 cm (median 178.4 cm). When weighted by
population size, the average height of a young European male can be estimated at 177.6 cm.
The geographical comparison of European samples (Fig. 1) shows that above average stature
(178+ cm) is typical for Northern/Central Europe and the Western Balkans (the area of the
Dinaric Alps). This agrees with observations of 20th century anthropologists (Coon, 1939;
Coon, 1970; Lundman, 1977). At present, the tallest nation in Europe (and also in the
world) are the Dutch (average male height 183.8 cm), followed by Montenegrins (183.2 cm)
and possibly Bosnians (182.5 cm) (Table 1). In contrast with these high values, the
shortest men in Europe can be found in Turkey (173.6 cm), Portugal (173.9 cm), Cyprus
(174.6 cm) and in economically underdeveloped nations of the Balkans and former Soviet
Union (mainly Albania, Moldova and the Caucasian republics). If we also took single
regions into account, the differences within Europe would be even greater. The first place
on the continent would belong to Herzegovinian highlanders (185.2 cm) and the second one
to Dalmatian Croats (183.8 cm).6 The shortest men live in Sardinia (171.3 cm; Sanna,
2002). Large differences in height exist even within some countries. For example, the
average height of Norwegian conscripts in the northern areas (the Finnmark county) is only
176.8 cm, but reaches 180.8 cm in the southern regions of Agder and Sogn og Fjordane,7
which is a very similar value like in Denmark and Sweden. In Finland, recruits are 178.6
cm tall on average, but men from the southwest of the country reach 180.7 cm (Saari et
al., 2010). Both in Norway and Finland, the national average is pulled down by the
northernmost regions that are inhabited by the Saami and are usually characterized by
below-average values around 177 cm. In Germany, the tallest men can be found in the
northwest, in areas adjacent to the Netherlands and Denmark (∼181 cm), while the shortest
men come from the southeast, east and southwest (∼179 cm) (Hiermeyer, 2009). Unusually
large differences are typical for Italy, where we can detect a 6.6 cm gap between Sardinia
and the northeastern region of Friuli-Venezia Giulia (Sanna, 2002). In the western
Balkans, geographical changes in body size are similarly striking, especially in Bosnia
and Herzegovina.

<hs>  The current state of the height trend</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The trend of increasing height has already stopped in Norway, Denmark, the Netherlands,
Slovakia and Germany. In Norway, military statistics date its cessation to late 1980s.
Since that time, the average height of Norwegian conscripts aged 18–19 years has
fluctuated between 179.4 and 179.9 cm.8 In Germany, the height of recruits has not changed
since the mid-1990s, when it reached ∼180 cm (J. Komlos–pers. communication). Denmark
Statistical Yearbooks also show a stagnation of the height of conscripts throughout the
2000s.9 In the Netherlands, national anthropometric surveys done in 1997 and 2009
documented the same height in young men aged 21 years (184.0 cm and 183.8 cm,
respectively; Schönbeck et al., 2013). According to preliminary results of the Slovakian
survey from 2011 (L. Ševčíková–pers. communication), the stature of Slovak males also
remained the same, 179.4 cm in 2001 and 179.3 cm in 2011. In contrast, the positive trend
of height still probably continues in Sweden and Iceland. The stature of Swedish
conscripts was growing throughout the 1990s and reached 180.2 cm in 2004, which was a 0.7
cm increase in comparison with 1994 (Werner, 2007). In 2008–2009, Swedish boys of
Scandinavian origin aged 17–20 years (n = 2408) from the Göteborg area were 181.4 cm tall
(Sjöberg et al., 2012). Although these results may not be perfectly comparable, it is
noteworthy that the mean in the latter study would decrease to 180.8 cm, if we included
boys with immigrant origin. These made up 13.4% of the whole sample and their mean height
was only 177.7 cm. This observation can lead to a speculation that the marked deceleration
of the height trend in some wealthy European countries may also be due to the growing
population of short-statured immigrants. Unfortunately, precise information on the
“immigration effect” is not routinely addressed in nationwide anthropometric studies.
Nevertheless, population means from an English health survey (2004) allow us to estimate
that immigrants and their descendants decreased the height of men in England by ca. −0.3
cm, from 177.5 to 177.2 cm.10 A certain stagnation or even a reversal of the height trend
can also be observed in other parts of Europe, but considering that it concerns relatively
less developed countries, with short population heights (e.g. Azerbaijan), it stems from
momentary economical hardships. The onset of the economic recession in the early 1990s was
particularly harsh in Lithuania, where it may have affected the youngest generation of
adult men, but not women: While in 2001, the average height of 18-year olds was 181.3 cm
in boys (n = 195) and 167.5 cm in girls (n = 278) (Tutkuviene, 2005), in 2008 the means in
the same age category in the area of Vilnius were 179.7 cm in boys (n = 250) and 167.9 cm
in girls (n = 263) (Suchomlinov and Tutkuviene, 2013). Since the economic situation in
Lithuania has dramatically improved during the last ∼15 years, the contemporary generation
of teenage boys could potentially exceed the value from 2001. In contrast, the fastest
pace of the height increase (≥1 cm/decade) can be observed in Ireland, Portugal, Spain,
Latvia, Belarus, Poland, Bosnia and Herzegovina, Croatia, Greece, Turkey and at least in
the southern parts of Italy. Interestingly, the adult male population in the Czech
Republic also continues to grow at a rate of ∼1 cm/decade. Our own observations were
supported by a recent cross-sectional survey of adolescents from Northern Moravia (Kutáč,
2013), in which 18-year old boys reached 181.0 cm (n = 169). In Estonia (Kaarma et al.,
2008) and Russia (RLMS survey), the pace of height increments in males can be estimated at
0.5 cm/decade. In Slovenia, the upward trend in 21-year olds has been slowing down, from
0.5 cm during 1992–2002 to only 0.3 cm during 2002–2012 (G. Starc–pers. communication). In
many of the wealthiest countries (Austria, France, Switzerland, United Kingdom and USA)
the increase is mostly steady, but slow. For example, the height of Austrian conscripts
increased by 0.5 cm in the period between 1991–1995 and 2001–2005 (E. Schober–pers.
communication). Similarly, the stature of Swiss conscripts increased by 0.6 cm between
1999 and 2009 (Staub et al., 2011). Approximately the same pace is typical for white
American men (Komlos and Lauderdale, 2007). In England, the height of men aged 25–34 years
stagnated at ∼176.5 cm during the 1990s, but then started to grow again around 2000 and
reached 177.6 cm in 2008–2009. Information from the southeastern part of Europe is much
scarcer, but DHS surveys show a moderate upward trend (∼0.8 cm/decade) in Albanian men
(Albania DHS survey, 2008–2009) and about 0.5 cm/decade in women from Armenia (Armenia DHS
survey, 2005) and Moldova (Moldova DHS survey, 2005).

<hs>  Positive relationship between GDP per capita and the height trend in Europe</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

As expected, the large regional differences in male height outlined in the Section 3.1
correlated with average GDP per capita (in USD, by purchasing power parity) according to
the World Bank (2000–2012) (r = 0.38; p = 0.011) (Table 2; Fig. 2). However, this
moderately strong relationship actually consists of two far narrower correlation lines in
the former communist “Eastern block” (r = 0.54; p = 0.008) and non-communist “Western
countries” (including Cyprus and Turkey) (r = 0.66; p < 0.001). The difference between
them is about 20 000 USD. In other words, some of the former “Eastern” countries reach the
same height like former “Western countries” despite ∼20,000 USD lower GDP and at the same
level of GDP, they are ca. 3 cm taller. These facts could imply that the trend of
increasing height in Europe continued uninterrupted on both sides of the “Iron curtain”,
irrespectively of the increasing gap in national wealth, and today's differences in height
were largely determined by regional differences existing in Europe at the end of the 19th
century. To test this hypothesis, we compared documented averages of young males from the
end of the 19th century with present values in 21 countries/regions (Fig. 3). This
comparison shows that the height of males in the eastern half of Europe (and even in
Southern Europe and the Netherlands) grew much faster than in the highly industrialized
Western Europe. For example, since the 1880s male height has increased by ca. 11 cm in
Great Britain and France, by 7.4 cm in Australia and by 8.1 cm in USA. In contrast, the
height of Czech and Dutch men has increased by 16.6 cm, Slovak men by 16.7 cm, Slovenian
men by 17.2 cm, Polish men by 17.5 cm and Dalmatian men by at least 18.3 cm. Furthermore,
the height of young men in these countries is currently higher than in Western Europe,
often very markedly. Apparently, this phenomenon can’t be explained by any economic
statistics. A very eccentric example emerged especially in former Yugoslavia, where Bosnia
and Herzegovina, Montenegro and Serbia reach much higher values of mean height than their
GDP would predict. After the exclusion of 6 successor states of former Yugoslavia, the
correlation with GDP per capita in the remaining 39 countries would steeply increase to r
= 0.58 (p < 0.001) and it would even reach r = 0.80 (p < 0.001) in 17 countries of the
former “Eastern block”. Remarkably, the huge decrease of height across the border of
Montenegro and Albania (at least -9 cm), at similar values of GDP per capita, has hardly
any parallel in other parts of the world, except a similar difference across the borders
of malnourished North Korea/South Korea (Kim et al., 2008; Pak, 2010) and USA/Mexico (Del-
Rio-Navarro et al., 2007; McDowell et al., 2008). Again, this points to the strong role of
some specific local factors. A very different situation can be observed in former
“Western” countries like Norway and Switzerland that have a much higher GDP per capita
than we would assume on the basis of the correlation line. Interestingly, the same applies
for the white population of USA, which is a phenomenon that is discussed (Komlos and
Lauderdale, 2007). It seems that economic growth in these countries must have outpaced the
positive height trend, but this fact still cannot explain, why the trend remains quite
slow or non-existent during the last decades.

<hs>  Health expenditure</hs>
  ~~~~~~~~~~~~~~~~~~

Besides GDP per capita, another moderately significant relationship (r = 0.35; p = 0.018)
was found between height and average health expenditure per capita (in USD, by purchasing
power parity) according to the World Bank (2000–2011). The general pattern was very
similar to that in Fig. 2, with two parallel and much stronger lines of correlation
consisting of the former “Eastern” (r = 0.59; p = 0.003) and “Western” (r = 0.56; p =
0.007) countries (Fig. 4). Wealthy countries spend more money on healthcare than poorer
countries, and USA is an anomaly in this regard. Relatively low expenditures on healthcare
are typical for the Balkans, Caucasian republics, the Mediterranean and former USSR
republics.

<hs>  Children's mortality under 5 years</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

A closely related factor, average children's mortality under 5 years (per 1000 live
births; according to the World Bank, 2000–2012), showed the highest impact on physical
growth out of all examined socioeconomic variables (r = − 0.61; p < 0.001) that would
persist even after the exclusion of an outlier—Azerbaijan (r = − 0.58; p < 0.001) (Fig.
5). Indeed, Hatton (2013) found that children's mortality (or a disease-free environment,
respectively) has had a far bigger influence on the positive height trend in Europe since
the mid-19th century than GDP per capita and other socioeconomic stats. Our data
nevertheless indicate that in contemporary Europe, children's mortality is a serious issue
only in some regions of the former USSR and the Balkans (mainly Azerbaijan, Georgia,
Turkey, Moldova, Armenia, Albania and Romania). When the death rate falls below 10 cases
per 1000 live births, this factor loses its predictive power, as shown by the sharp
difference between correlation coefficients in the former “Eastern” block (r = − 0.75; p <
0.001) and “Western” countries (r = − 0.48; p = 0.022).

<hs>  Gini index</hs>
  ~~~~~~~~~~

The Gini index of social inequality (the latest available year after the CIA World
Factbook, 1997–2011) also appeared to be a significant, negative variable (r = − 0.40; p =
0.007) (Fig. 6). The lowest values of the Gini index (i.e. the highest levels of social
equality) are typical for Northern/Central Europe, while the highest Gini indices (the
biggest social differences) can be found mainly in the Balkans, former USSR, and also in
the United Kingdom and USA. A higher Gini average (33.2) indicates that social differences
in countries of the former “Eastern block” are somewhat more accentuated, but they have no
relationship to male stature (r = − 0.30; p = 0.16), most probably because of outliers in
the least developed regions, where the Gini index recedes to the background at generally
high levels of poverty. In contrast, the Gini index in “Western” countries is lower on
average (31.5), but it does play some role in this regard (r = − 0.52; p = 0.013), mainly
because of the wide polarity between egalitarian societies of Northern/Central Europe on
one hand, and more socially stratified countries like USA, UK, Portugal and Turkey on the
other hand. In general, social inequality tended to increase with decreasing GDP per
capita (r = − 0.31; p = 0.038) and it also correlated with higher children's mortality
rates (r = 0.39; p = 0.008). It is understandable that when lower social classes suffer
from an uneven distribution of wealth, they are likely to reach lower height on average
and pull the national mean down. A huge role of socioeconomic differences can be
demonstrated on some examples from the Balkans, where it concerns mainly the contrast
between urban and rural populations. For example, male height in Romania can range from
168.2 cm in rural areas of Suceava county up to 179.5 cm in middle-sized towns of the same
region (Vasilov, 2001). Nevertheless, male height in Lithuania, Latvia and Bosnia and
Herzegovina is still above-average, despite rather high Gini indices.

<hs>  Urbanization (% urban population)</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The effect of urbanization (measured as the proportion of the urban population according
to the World Bank, 2000–2012) was quite low (r = 0.30; p = 0.046), when Europe is viewed
as a whole, but its role increases dramatically, when only former “Western countries” are
taken into account (r = 0.55; p = 0.007), or when former Yugoslavia is excluded (r = 0.56;
p < 0.001) (Appendix Fig. 1). This is also reflected by the high association between
urbanization and GDP per capita (r = 0.69; p < 0.001) (Appendix Table 1). In the former
“Eastern block”, urbanization in the above mentioned period was much lower (60.5% vs.
77.0% in the “West”) and has no relationship to stature (r = 0.14; p = 0.53). Based on our
data, it seems that the level of urbanization starts to affect stature only after more
than ∼70% population is concentrated in cities.

<hs>  Total fertility</hs>
  ~~~~~~~~~~~~~~~

The analysis of fertility (total number of children per woman) was based on the statistics
from the World Bank (2000–2011). The presumption is that if the number of children is low,
the expenditure of parents per a child can increase, and hence living conditions for its
development improve. This factor apparently played an important role in the acceleration
of the height trend in Europe in the past (Hatton and Bray, 2010), but this does not seem
to be the case in contemporary Europe (r = − 0.11; p = 0.47) and especially in “Western”
countries (r = 0.12; p = 0.60) (Appendix Fig. 2). The correlation coefficient was medium
high only in former “Eastern” countries (r = − 0.47; p = 0.024), largely due to higher
birth rates in economically disadvantaged regions of the Balkans and former USSR.
Considering that birth rates are already very low in all regions of Europe, height
differences among nations are unlikely to be influenced by this variable. To the contrary,
it is possible that in the future, height will correlate positively with higher fertility,
as indicated by the positive relationship of fertility with GDP per capita (r = 0.33; p =
0.025), health expenditure (r = 0.36; p = 0.016) and urbanization (r = 0.40; p = 0.006)
(Appendix Table 1).

<hs>  Nutrition</hs>
  ~~~~~~~~~

The available data on protein consumption from the FAOSTAT database (2000–2009) show that
male stature generally correlates positively with animal proteins (r = 0.41; p = 0.005),
particularly with proteins from milk products in general (r = 0.47; p = 0.001), cheese (r
= 0.44; p = 0.002), pork meat (r = 0.42; p = 0.004) and fish (r = 0.33; p = 0.028).11 In
plant proteins, the effect was clearly negative (r = − 0.50; p < 0.001), and was
particularly strong in proteins from wheat (r = − 0.68; p < 0.001) (Fig. 7) and cereals in
general (r = − 0.59; p < 0.001), but partly even in rice (r = − 0.38; p = 0.01) and
vegetables (r = − 0.35; p = 0.017) (Table 3). Total protein consumption is quite an
insignificant dietary indicator, because its relationship to male stature is very weak (r
= 0.19; p = 0.20). When we combined the intake of proteins with the highest r-values, the
correlation coefficients further increased, as evidenced by the relationship betwen height
and the total consumption of proteins from milk products and pork meat (r = 0.55; p <
0.001), or from milk products, pork meat and fish (r = 0.56; p < 0.001) (Fig. 8). All
these comparisons still failed to explain the extreme height of the Dutch. The secret of
the tall Dutch stature emerged only after we plotted the total consumption of proteins
from milk products, pork meat and fish against the consumption of wheat proteins. This
“protein index” was the strongest predictor of male height in our study, when all 45
countries were included (r = 0.72; p < 0.001) (Fig. 9).12 Without former Yugoslavia, the
correlation further increased to r = 0.77. The ratio between milk and wheat proteins gave
almost the same result (r = 0.71; p < 0.001). These findings are logical, because
according to the amino acid score (AAS, the proportion of the worst represented amino
acid), wheat contains one of the poorest proteins among all kinds of food due to a severe
deficit of lysine, whereas animal proteins contain one of the very best proteins (see
Appendix Table 2 and further e.g. Milford, 2012; FAO Expert Consultation, 2013).
Furthermore, the digestibility of protein from plant foods is between 80% and 90%, while
the digestibility of animal protein is higher, usually ∼95%, and can reach 100% in boiled
meat.13 Therefore, the PDCAAS (Protein Digestibility Corrected Amino Acid Score, i.e. true
protein quality) of plant proteins is even lower and it is mainly the ratio between the
best and worst proteins that determines the overall level of the diet.14

<hs>  Implications for rational nutritional programs</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The fundamental role of nutrition among exogenous variables influencing male stature has
very important implications. While many economic and social factors are usually beyond an
individual's direct control (personal income, total fertility and living in urban areas
being rather exceptions), nutrition is a matter of personal choice. It is true that the
accessibility of certain foodstuffs is limited by national wealth (GDP per capita), but
the relationship is not as high as we would expect. GDP per capita has the most direct
influence on the total consumption of animal protein (r = 0.82), meat (r = 0.78), cheese
(r = 0.75) and exotic fruits like pineapples, oranges and bananas (r≥0.67), but not so
much on the “protein index” (r = 0.57; p < 0.001). This shows that nutrition in all
countries could be significantly improved via rational dietary guidelines, irrespectively
of economic indicators. In this context, it should be noted that the quality of proteins
(expressed as the “protein index”) in the wealthiest nations of European descent has a
tendency to deteriorate during the last 2–3 decades (Fig. 9 and Appendix Fig. 3). This
trend is characterized by a partial decrease in the consumption of milk products, beef and
pork meat, and increasing consumption rates of cheese, poultry and cereals. In contrast,
the quality of nutrition in the Mediterranean and some countries of the former Eastern
block has been improving (Appendix Fig. 4). In the light of these findings, it is
understandable, why other wealthy nations haven’t reached the height standard seen in the
Netherlands and why their positive height trend slowed down or stopped. We suspect that
these negative tendencies are due to the combination of the inadequate “fast-food”
nutrition with some misleading dietary guidelines such as “modern healthy eating plates”
of the Harvard School of Public Health. These are currently promoted by certain public
initiatives in Czech schools and empasize vegetables and whole grains at the expense of
animal proteins, while recommending to limit milk intake.15 Although some of these
recommendations could certainly improve overall health in adults, our calculations based
on the FAOSTAT data show that they should be viewed as detrimental for the healthy
development of children. The possible health risks of a diet based on high-quality animal
proteins seem to be exaggerated as well and we intend to address all important issues
related to height and nutrition in a more detailed paper, based on our own research using
actual statistics of the incidence/prevalence of cancer and cardiovascular diseases in
Europe and long-term averages of FAOSTAT data (1993–2009).

<hs>  Y haplogroups I-M170 and R1b-U106: possible genetic determinants of extreme tallness in Europe</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Although the documented differences in male stature in European nations can largely be
explained by nutrition and other exogenous factors, it is remarkable that the picture in
Fig. 1 strikingly resembles the distribution of Y haplogroup I-M170 (Fig. 10a). Apart from
a regional anomaly in Sardinia (sub-branch I2a1a-M26), this male genetic lineage has two
frequency peaks, from which one is located in Scandinavia and northern Germany (I1-M253
and I2a2-M436), and the second one in the Dinaric Alps in Bosnia and Herzegovina
(I2a1b-M423).16 In other words, these are exactly the regions that are characterized by
unusual tallness. The correlation between the frequency of I-M170 and male height in 43
European countries (including USA) is indeed highly statistically significant (r = 0.65; p
< 0.001) (Fig. 11a, Table 4). Furthermore, frequencies of Paleolithic Y haplogroups in
Northeastern Europe are improbably low, being distorted by the genetic drift of N1c-M46, a
paternal marker of Ugrofinian hunter-gatherers. After the exclusion of N1c-M46 from the
genetic profile of the Baltic states and Finland, the r-value would further slightly rise
to 0.67 (p < 0.001). These relationships strongly suggest that extraordinary
predispositions for tallness were already present in the Upper Paleolithic groups that had
once brought this lineage from the Near East to Europe. The most frequent Y haplogroup of
the western and southwestern part of Europe is R1b-S116 (R1b1a2a1a2-S116) that reaches
maximum frequencies in Ireland (82%), Britain, France and on the Iberian peninsula (∼50%),
and is in all likehood tied with the post-glacial expansion of the Magdalenian culture
from the glacial refugium in southern France/Cantabria (Fig. 10b).17 As already mentioned,
Mesolithic skeletons in Western Europe were typically petite (∼163 cm) (Formicola and
Giannecchini, 1999), which could imply that this haplogroup would be connected with below
average statures. When we omitted 14 countries of Eastern and Southeastern Europe, where
the frequencies of R1b-S116 are mostly close to zero, the relationship between R1b-S116
and male height reached statistical significance (r = − 0.48; p = 0.049) (Appendix Fig.
5). Therefore, the frequency of R1b-S116 may limit the future potential of physical
stature. A related branch, R1b-U106 (R1b1a2a1a1-U106), apparently has a very different
history and is typical for Germanic speaking nations, with a frequency peak in Friesland
(∼43%). Its correlation with male height in 34 European countries was rather moderate (r =
0.49; p = 0.003), but increased to 0.60 (p = 0.007) without Eastern and Southeastern
Europe. Visually, the distribution of this haplogroup resembles that of I1-M253 and
I2a2-M436 in Northern and Central Europe, which would indicate that they shared a common
local history, very different from R1b-S116. This assumption is also supported by the fact
that out of all examined genetic lineages in Europe, combined frequencies of R1b-U106 and
I-M170 have the strongest relationship to male stature (r = 0.75; p < 0.001 in 34
countries) (Fig. 11b and Appendix Fig. 6). The fourth most important Y haplogroup
endogenous to Upper Paleolithic Europe, R1a-M420, is typical for Slavic nations (with ∼50%
frequency in Belarussians and Ukrainians, and 57% in Poles) and has a steeply curvilinear
relationship with height that peaks in the case of Poland (178.5 cm) and then abruptly
decreases, largely due to a rising proportion of I-M170 in the genetic pool of tall
nations. As a result, it is not a good predictor of male height (r = 0.19; p = 0.21)
(Appendix Fig. 7), but combined frequencies of I-M170 and R1a-M420 reach statistical
significance (r = 0.52; p < 0.001) (Appendix Fig. 8). After the exclusion of N1c-M46, the
frequency of R1a-M420 in the Baltic states would rise above neighbouring Slavic nations
(up to 66.5% in Latvia), but its predictive power still would lag behind I-M170 (r = 0.25;
p = 0.11). Such a result implies that this lineage may have a moderate position in Europe,
as for genetic predispositions for height. Y haplogroups E-M96, G-M201 and J-P209
represent the most important non-indigenous, post-Mesolithic lineages that spread to
Europe mainly during the Neolithic expansion from the Near East (6th millenium BC).
Expectably, their combined frequencies are the highest in the southeastern part of Europe
(>40%) and decrease below 5% in the most remote areas of the continent such as Ireland,
Scotland and the Baltic region (Appendix Fig. 9). Their relationship to male stature was
markedly negative (r = − 0.64; p < 0.001) (Appendix Fig. 10) and remained significant even
after an adjustment for GDP (r = − 0.57; p < 0.001) or the “protein index” (r = − 0.40; p
= 0.009). This result indicates that the extremely small statures of early
agriculturalists stemmed both from severe undernutrition and genetics.

<hs>  Multiple regression analyses of socioeconomic, nutritional and genetic data</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Considering that data on the frequencies of I-M170, R1a-M420 and three post-Mesolithic
lineages (E-M96, G-M201 and J-P209) were available from 43 countries (except Australia and
New Zealand), we included these 43 countries into a series of multiple regression
analyses. When we examined the relationship between male height and 6 socioeconomic
variables previously discussed above, a forward multiple regression identified children's
mortality and the Gini index as the only factors contributing to a fully saturated model
(R = 0.63, adj. R2 = 0.37; p < 0.001). Nutritional factors included into a forward
stepwise regression consisted of the “protein index” and 9 significant (p < 0.05) protein
sources with a daily intake higher than 3.0 g protein per capita (see Table 3). Except
pork meat, all of them played an important role (R = 0.89, adj. R2 = 0.73; p < 0.001).
Among three genetic factors, only two (I-M170 and E + G + J) turned out to be meaningful
(R = 0.76, adj. R2 = 0.56; p < 0.001). Subsequently we made a standard regression analysis
that included all 17 meaningful variables significantly related to stature (p < 0.05): two
genetic factors (I-M170, E + G + J), five socioeconomic factors and 10 nutritional
factors. Here, five variables turned out to be statistically significant (Table 5a), but
the low values of tolerance indicated a very high degree of multicollinearity. A simpler,
fully saturated model based on a forward stepwise regression (R = 0.89, adj. R2 = 0.75, p
< 0.001) consisted of eight variables (Table 5b).18 The “protein index” determined in this
study was by far the most important, followed by Y haplogroup I-M170 and cheese (the
source of the most concentrated milk proteins).19 Interestingly, this model also explained
the seemingly outlier position of the Dinaric countries and the most important factor here
was the inclusion of the genetic component (I-M170) (Appendix Table 4 and Fig. 11). When
examining the causes of the unexpected gap in height between “Eastern” and “Western”
countries in Fig. 2, we observed that out of all variables examined in this study, Y
haplogroup I-M170 and the “protein index” had the most marked effect on the increase of
R-values (to R = 0.71, adj. R2 = 0.48 and R = 0.73, adj. R2 = 0.50, respectively) and
hence a narrowing of this gap, when added as independent variables into a multiple
regression that incorporated male height and GDP per capita. In other words, the tallest
countries of the former Eastern block enjoy a relatively high level of nutrition that is
often better than in “Western” countries with similar or higher GDP values. In addition,
their means of male height are further elevated due to genetic factors, which especially
applies for former Yugoslavia.

<hs>  The role of lactose tolerance: another possible genetic predictor of height in Northern and Central Europe?</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

The fundamental role of milk in the nutrition of European nations stems from the high
prevalence of lactose tolerance—a very valuable genetic trait allowing a sufficient intake
of milk even during adulthood. Although many scientists are still not certain about the
evolutionary role of lactose tolerance in Europe, the findings of this study show that the
ability to consume milk must have been a tremendeous advantage, because it opened up an
additional source of nutrition that not only guaranteed survival in the periods of food
shortage, but contained nutrients right of the highest natural quality. Interestingly, the
correlation of lactose tolerance with the consumption of whole milk (r = 0.10; p = 0.62)
and milk products in general (r = 0.59; p = 0.001) was weaker than that between lactose
tolerance and male height (r = 0.71; p < 0.001) (Fig. 12). This is the exact opposite of
what we would expect. Considering that lactose tolerance is a genetic trait, it is
possible that it may correlate with certain genes that determine tall stature. When
examining the relationship between lactose tolerance and frequencies of Y haplogroups, we
noticed a very high association of lactose tolerance with the combined frequency of I-M170
and R1b-U106 (r = 0.74; p <0.001 in 23 countries) (Appendix Fig. 12). The correlation
coefficient further increased to r = 0.78 (p < 0.001, 21 countries), when R1b-S116 was
added, although it overestimated lactose tolerance in R1b-S116-rich areas such as the
British Isles, France, Spain and Italy (Appendix Fig. 13 and 14). Based on these results,
we hypothesize that the spread of lactose tolerance started from the Northwest European
territory between Belgium and Scandinavia, which is the presumed area of origin of the
Funnelbeaker culture during the 4th millenium BC (Appendix Fig. 15a). These populations
probably carried Y haplogroups I-M170 (I1-M253 and I2a2-M436), R1b-U106 and partly
R1b-S116. The successor Corded Ware populations most likely expanded from present-day
Poland during the 3rd millenium BC and their genetic composition may have been somewhat
different. In any case, contrary to some assumptions, which are also based on limited
archeogenetic data (Haak et al., 2008), the distribution of lactose tolerance does not
seem to be related to Y haplogroup R1a-M420 (r = − 0.10; p = 0.62 in 26 countries), and
this picture would hardly change even when missing data from Latvia and Belarus were
added. Obviously, if Corded Ware populations consisted of R1a-M420 males, they were not
closely related to the earliest carriers of the lactose tolerance genes. Alternatively,
they may have belonged to some minor subbranches of R1a-M420.20 Besides that, the spread
of lactose tolerance in Western Europe and in the British Isles must have been tied with
some other cultural circle, perhaps the Bell-Beaker culture during the second half of the
3rd millenium BC (Appendix Fig. 15b). Similarly, lactose tolerance can’t be connected with
Near Eastern agriculturalists, i.e. Y haplogroups E-M96, G-M201 and J-P209 (r = − 0.73; p
< 0.001), despite computer simulations showing that genes of lactose tolerance were
originally acquired from agricultural populations in Central Europe (Itan et al., 2009).

<h>CONCLUSION</h>
----------

The dramatic increase of height in Europe starting during the late 19th century is closely
linked with the beneficial effect of the industrial revolution. Our comparisons show that
this effect is manifested in generally higher standards of living, better healthcare,
lower children's mortality, lower fertility rates, higher levels of urbanization, higher
social equality and access to superior nutrition containing high-quality animal proteins.
In the past, some of these factors may have been more important for a healthy physical
growth than they are today and some of them are important only in certain regions, but in
general, the most important exogenous factor that impacts height of contemporary European
nations is nutrition. More concretely, it is the ratio between proteins of the highest
quality (mainly from milk, pork meat and fish) and the lowest quality (i.e. plant proteins
in general, but particularly wheat proteins). Besides that, we discovered a similarly
strong connection between male height and the frequency of certain genetic lineages (Y
haplogroups), which suggests that with the gradual increase of living standards, genetic
factors will increasingly be getting to the foreground. Even today, many wealthy nations
of West European descent are ca. 3 cm smaller than much poorer countries of the former
Eastern block with the same nutritional statistics. Another evidence for this genetic
hypothesis recently appeared in the study of Turchin et al. (2012), who found
systematically higher presence of alleles associated with increased height in US whites of
North European ancestry than in Spaniards. Remarkably, the quality of nutrition in the
wealthiest countries shows signs of a marked deterioration, as indicated by the decreasing
values of the “protein index”. This can illuminate the recent deceleration/cessation of
the positive height trend in countries like USA, Norway, Denmark or Germany, which was
routinely explained as the exhaustion of the genetic potential. In our opinion, this
assumption is still premature and with the new improvement of nutritional standards, some
increase still can be expected. A very specific case is that of Dinaric highlanders, who
are as tall or even taller than the wealthiest nations, in spite of considerably lower
living and nutritional standards. However, their seemingly outlier position can be
explained by strong genetic predispositions. In the near future, we want to focus on this
problem in detail via our planned field project directly in the Dinaric Alps, in
collaboration with the University of Montenegro.


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<ART>Time consistency and time invariance in collective intertemporal choice
=======================================================================

Authors: Antony Millner, Geoffrey Heal
DOI: 10.1016/j.jet.2018.03.002
Year: 2018  |  Pages: 158-169
ASJC codes: 2002
Keywords: Collective decisions, Intertemporal choice, Time consistency

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

Recent work on collective intertemporal choice suggests that non-dictatorial social preferences are generically time inconsistent. We argue that this claim conflates time consistency with two distinct properties of preferences: stationarity and time invariance. While time invariance and stationarity together imply time consistency, the converse does not hold. Although non-dictatorial social preferences cannot be stationary, they may be time consistent if time invariance is abandoned. If individuals are discounted utilitarians, revealed preference provides no guidance on whether social preferences should be time consistent or time invariant. Nevertheless, we argue that time invariant social preferences are often normatively and descriptively problematic.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

Many important decisions in economic life require groups of people with heterogeneous time
preferences to implement a collective consumption plan. Examples abound: families must
decide on savings and intra-household resource allocation, partners in a firm must decide
how to distribute profits between payouts to themselves and capital investments,
communities with property rights over a natural resource must decide on an extraction
plan, and resource rich countries must decide how to consume the proceeds from their
sovereign wealth funds. In each of these examples an asset is held in common and is
consumed dynamically over time, and the stake-holders in the decision very often have
heterogeneous time preferences (Frederick et al., 2002). How should such decisions be
evaluated and made, given people's different attitudes to time? Recent theoretical and
applied work (Jackson and Yariv, 2014, 2015; Adams et al., 2014) suggests that any attempt
to make such collective intertemporal choices in a non-dictatorial fashion is doomed to
confront a time inconsistency problem (see also earlier observations by Marglin, 1963;
Feldstein, 1964; and Zuber, 2011). This paper argues that this finding is due to a
conflation of time consistency with two a priori distinct properties of preferences:
Stationarity and Time Invariance. Stationarity, introduced by Koopmans (1960), is an
independence property of preferences, while time invariance requires preferences over
future consumption streams to be the same in each evaluation period (this does not rule
out preference reversals – quasi-hyperbolic time preferences, for example, are time
invariant). Jackson and Yariv (2014, 2015), for example, show a necessary conflict between
collective intertemporal choice and stationarity, but assume that social preferences must
be time invariant. Yet while time invariance and stationarity together imply time
consistency, the converse does not hold; time invariance is not required for time
consistency. If the differences between these three properties of intertemporal
preferences are made explicit it becomes clear that time consistent collective
intertemporal choice is possible. The differences between time consistent and time
invariant social preferences are particularly subtle when individuals' preferences are
discounted utilitarian, as is commonly assumed in the literature on the aggregation of
time preferences. In this case, time consistency and time invariance are equivalent
properties of individuals' preferences1 (Halevy, 2015), but not of social preferences. We
show that if individuals have heterogeneous discount factors, and social preferences are
utilitarian and non-dictatorial, these preferences may be time consistent or time
invariant, but not both. Since these properties are indistinguishable for discounted
utilitarian individuals, but not for social preferences, the choice to impose one or the
other property at the social level is ultimately a normative one – neither choice is more
or less consistent with individuals' preferences. We argue however that time invariance is
likely to be a problematic feature of social preferences – both normatively and
descriptively – for within-group intertemporal choice. Time invariance may however be more
descriptively plausible for between-group choice, as might occur in intergenerational
decision-making. We relate these observations to the empirical literature that seeks to
test the time consistency of household behaviour, suggesting that the definition of time
consistency it employs is too restrictive.

<h>TIME CONSISTENCY, TIME INVARIANCE, AND STATIONARITY</h>
---------------------------------------------------

To make our argument we begin by providing definitions of three distinct properties of
intertemporal preferences: time consistency, time invariance, and stationarity. Once we
have defined these properties, it will immediately be clear that any two of them implies
the third, as observed in a simplified setting by Halevy (2015). We then show that the
notion of time consistency used by e.g. Jackson and Yariv (2014, 2015); Adams et al.
(2014) is in fact the conjunction of time invariance and stationarity. Time invariance and
stationarity imply time consistency, but the converse does not hold. “[Stationarity] does
not imply that, after one period has elapsed, the ordering then applicable to the ‘then’
future will be the same as that now applicable to the ‘present’ future. All postulates are
concerned with only one ordering, namely that guiding decisions to be taken in the
present.” – Koopmans et al. (1964) Halevy (2015) has observed in a simplified setting3
that any two of the three properties in Definition 1 implies the third. Inspection of the
definitions shows that this observation holds in general.

<h>TIME CONSISTENT UTILITARIAN SOCIAL PREFERENCES</h>
----------------------------------------------

If utilitarian social preferences are time consistent and non-dictatorial, the following
interpretations of (7) are equivalent: Individuals have forward-looking welfare measures,
and social preferences have τ-dependent welfare weights (8). Individuals experience
lifetime utility, and welfare weights are constant.

<h>TIME CONSISTENCY OR TIME INVARIANCE?</h>
------------------------------------

We have argued that there is no conflict between time consistency and non-dictatorial
collective intertemporal choice, provided that time invariance is abandoned. Should we
nevertheless insist that social preferences be time invariant, thus ruling out the
possibility of time consistency? Given that revealed preference cannot tell us which
property to adopt if individual preferences are discounted utilitarian, how should we make
this choice? In order to demonstrate what is at stake when choosing to model social
preferences as time invariant it is helpful to consider the following stylized scenario:
Ada and Bertha are identical twins; both are childless, single, and have identical wealth.
On their 60th birthday they receive news that a distant cousin they've never met has died,
and they will inherit his fortune. Their cousin died intestate, so there is no will to
specify how the bequest should be divided between them. Ada is naturally impatient, while
Bertha is patient. How should a utilitarian social planner allocate the bequest between
them? Suppose that the planner is time consistent. In this case first best intertemporal
allocations can be decentralized by establishing property rights over the bequest, and
then allowing each sister to consume her share as she pleases. Suppose that the planner's
ethics dictate that an equal share of the bequest be given to each sister. The planner
makes this allocation, and walks away happy in the knowledge that she need never revisit
this decision. Now consider a time invariant planner, and suppose that she also initially
allocates equal shares to the sisters, before departing on other business, never intending
to return. To her surprise however, the planner is asked to revisit the sisters 10 years
later and assess their well-being. Ada has led a wild life in the intervening decade,
consuming her inheritance much faster than Bertha. But the planner asks herself: what has
changed since the sisters were 60? Although Ada has had a better life than Bertha, this is
in the past and can't be changed. Since the circumstances are the same, except that the
sisters happen to be 10 years older, the planner seizes some of Bertha's carefully saved
cash, and reallocates it to Ada, so that their holdings of what remains of the bequest are
again equal. Ada immediately spends her new wealth on fast cars and fancy footwear, while
Bertha continues to put something away for a rainy day. Are there situations where time
invariance might seem a more appropriate assumption than time consistency? We believe that
modeling social preferences as time invariant might be more plausible if we are attempting
to describe conflicts between successive groups of different people, as might occur in
e.g. intergenerational decision-making. To illustrate, consider the following example: A
nation discovers an enormous oil deposit in its territorial waters. The deposit is large
enough to generate rents for generations to come, which will be invested in public goods
that benefit all citizens equally. Citizens are born in different time periods, and have
finite lives.8 Suppose that each citizen is either Avaricious (i.e. favours a high
intergenerational discount rate), or Benevolent (i.e. favours a low intergenerational
discount rate). In each period the currently living citizens must decide how much oil to
extract. How is this likely to be done? The crucial difference between the ‘twins’ and
‘oil’ scenarios we have sketched is that in the case of the twins we were concerned with
intertemporal distribution within a fixed group of people over time, whereas in the oil
case we were concerned with intertemporal distribution between different groups of people.
In the former case all agents who are affected by a decision are present at all points of
time, whereas in the latter only a subset of agents affected by a decision are present at
each point in time. Time consistency seems a much more plausible descriptive property of
social preferences than time invariance in the former case, since the ahistorical nature
of time invariant preferences would be seen as deeply unfair by current agents. In the
case of between-group choice however, although time invariance may do violence to the
preferences of previous or successive groups, these individuals have no voice in current
decision processes. As a descriptive matter, it seems more likely that the interests of
past and future groups are only relevant insofar as current decision-makers account for
them. To our minds this makes time invariance a more plausible descriptive modeling
assumption in this case. Of course, this argument makes no claims about the normative
status of time invariance as a property of social welfare criteria.

<h>IMPLICATIONS FOR THE EMPIRICAL LITERATURE</h>
-----------------------------------------

While we find time invariance to be a not implausible descriptive property in between-
group choice, the empirical literature focusses exclusively on within-group choice. Our
hypothesis that time consistent, but non-invariant, social preferences are likely to
prevail in this case receives support from the innovative study of household consumption
behaviour in Adams et al. (2014). Although they strongly reject the hypothesis that
household behaviour can be described by time invariant and time consistent preferences of
the form (11), they find considerable support for the hypothesis that household
consumption behaviour can be rationalized by time consistent social preferences with time
varying welfare weights (8). Adams et al. (2014) refer to this as the ‘full efficiency’
model, and claim that this identifies individual discount rate heterogeneity as a source
of household time inconsistency. Yet the appropriate interpretation of these findings is
that collective choices can often be rationalized by a time consistent utilitarian model,
provided that household preferences account for the cumulative lifetime utility
experienced by each household member.


<h>REFERENCES</h>
----------

  [1] Abi Adams, Laurens Cherchye, Bram De Rock, Ewout Verriest. Consume now or later? Time inconsistency, collective choice, and revealed preference. doi:10.1257/aer.104.12.4147
  [2] Andrew Caplin, John Leahy. The social discount rate. doi:10.1086/424740
  [4] Shane Frederick, George Loewenstein, Ted O'Donoghue. Time discounting and time preference: A critical review. doi:10.1257/jel.40.2.351
  [5] Yoram Halevy. Time Consistency: Stationarity and Time Invariance. doi:10.3982/ECTA10872
  [6] Matthew O. Jackson, Leeat Yariv. Present bias and collective dynamic choice in the lab?. doi:10.1257/aer.104.12.4184
  [7] Matthew O. Jackson, Leeat Yariv. Collective dynamic choice: The necessity of time inconsistency. doi:10.1257/mic.20140161
  [10] Stephen A. Marglin. The social rate of discount and the optimal rate of investment. doi:10.2307/1879374
  [11] R. H. Strotz. Myopia and inconsistency in dynamic utility maximization. doi:10.2307/2295722
  [12] Stéphane Zuber. The aggregation of preferences: Can we ignore the past?. doi:10.1007/s11238-010-9225-4
<ART>U.S. obesity as delayed effect of excess sugar
==============================================

Authors: R. Alexander Bentley, Damian J. Ruck, Hillary N. Fouts
DOI: 10.1016/j.ehb.2019.100818
Year: 2020
ASJC codes: 2001
Keywords: High-fructose corn syrup, Obesity, Socioeconomic status, Sugar

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

In the last century, U.S. diets were transformed, including the addition of sugars to industrially-processed foods. While excess sugar has often been implicated in the dramatic increase in U.S. adult obesity over the past 30 years, an unexplained question is why the increase in obesity took place many years after the increases in U.S. sugar consumption. To address this, here we explain adult obesity increase as the cumulative effect of increased sugar calories consumed over time. In our model, which uses annual data on U.S. sugar consumption as the input variable, each age cohort inherits the obesity rate in the previous year plus a simple function of the mean excess sugar consumed in the current year. This simple model replicates three aspects of the data: (a) the delayed timing and magnitude of the increase in average U.S. adult obesity (from about 15% in 1970 to almost 40% by 2015); (b) the increase of obesity rates by age group (reaching 47% obesity by age 50) for the year 2015 in a well-documented U.S. state; and (c) the pre-adult increase of obesity rates by several percent from 1988 to the mid-2000s, and subsequent modest decline in obesity rates among younger children since the mid-2000s. Under this model, the sharp rise in adult obesity after 1990 reflects the delayed effects of added sugar calories consumed among children of the 1970s and 1980s.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

In approximately two generations, obesity has become an epidemic across the Developed
world (Goryakin et al., 2017). Worldwide, obesity nearly tripled between 1975 and 2016; by
2016, more than 650 million adults were obese, about 13% of the world's adult population
(World Health Organization, 2018). Among children and adolescents aged 5–19, the global
obesity rate rose from 1% in 1975 to 6% of girls and 8% of boys in 2016 (World Health
Organization, 2018). Although the rise in U.S. obesity dates to the mid 20th century
(Sobal and Stunkard, 1989), the most substantial and rapid increase in adult obesity has
occurred over the past 30 years (Cook et al., 2017; Dwyer-Lindgren et al., 2013; Flegal et
al., 2016; Kranjac and Wagmiller, 2016; Ogden et al., 2014). From 1990 to 2016 the
national adult obesity rate almost doubled; in certain U.S. states (WV, MS, AK, LA, AL,
KY, SC) it nearly tripled, from about an eighth of the population to more than a third.
There are clearly many contributors to the obesity crisis, many of which have been studied
over past decades through randomized control trials and through population-scale
statistical analyses (Hruby and Hu, 2015; Rippe, 2013). Among the major factors in this
recent increase, one is age. In the U.S. in 2015–16, obesity prevalence was about 36%
among adults aged 20–39 years, 43% for 40–59 years, and 41% for 60 and older (Centers for
Disease Control & Prevention, 2017a). In 2015–2016, nearly 20% of 6–19 year-olds were
obese (Hales et al., 2017). Data from the state of Wisconsin (Wisconsin Health Atlas,
2019), which ranks near the middle of U.S. states in obesity, document the age profiles in
more detail for the year 2015, showing the continuous rise in obesity from age two years
to middle age, where the obesity rate plateaus near 47%, before falling off among those
aged over 75 years (Fig. 1a). The increase in obesity through childhood is a recent
phenomenon, however; in the U.S. in 1970s there was an average decrease in obesity rate
from ages two to nineteen (Wang and Beydoun, 2002). Another major factor is socioeconomic
status (Hruschka, 2012; Smith, 2017; Sobal and Stunkard, 1989; Tafreschi, 2015; Salmasi
and Celidon, 2017; Villar and Quintana-Domeque, 2009). In the U.S., the increase in
obesity rate between 1990 and 2015 has correlated inversely with median household income
(Bentley et al., 2018). Looking at county-scale obesity rates from 2004 to 2013 (Centers
for Disease Control & Prevention, 2017b), the average obesity among the 100 poorest
counties in the U.S. increased from about 29.9% to 36.5%, but only from 21.2% to 24.6%
among the 100 richest counties. As obesity rates have increased faster in poor
communities, a likely driver has been the lowering cost of food calories (Mattson et al.,
2014; Mullan et al., 2017), including sugar-sweetened beverages (Basu et al., 2013a; Hu
and Malik, 2010; Johnson et al., 2007, 2016; Malik et al., 2006; Shang et al., 2012; Song
et al., 2012; Wang et al., 2008). Since 1970, when high-fructose corn syrup (HCFS) was
introduced at commercial scale into processed foods and sugar-sweetened beverages (SSBs),
consumption of HFCS increased from virtually zero in 1970 to over 60 pounds per capita
annually in 2000 (Gerrior et al., 2004). Overall, the consumption of added sugars
increased from about 70 pounds per person annually in 1970 (340 cal/day) to almost 90
pounds per capita (440 cal/day) by the late 1990s (Fig. 1b). By the 2000s, the top 20% of
consumers of caloric sweeteners were ingesting over 300 kcal from HFCS per day (Bray et
al., 2004). Much of the rise in total added sugar consumption between 1970 and 2000 is
attributable to HFCS (Fig. 1b), often in SSBs that contribute additional calories without
suppressing appetite for the intake of other foods (Almiron-Roig et al., 2013; Mattes and
Campbell, 2009). The correlation between the increased consumption of added sugars in U.S.
foods and the rise of obesity (Fig. 1b) has been recognized (Bray et al., 2004; Basu et
al., 2013b; Lustig et al., 2015), even by the sweetener industry (Corn Refiners
Association, 2006). Consequently, sugar consumption has been hypothesized to be a primary
driver of the recent obesity increase (Basu et al., 2013a,b; Bray et al., 2004; Bray,
2007; Lustig et al., 2015; Nielsen et al., 2002; Nielsen and Popkin, 2004; Popkin and
Hawkes, 2016). Time series data from 75 countries, for example, indicate that a 1% rise in
soft drink consumption in a country predicts about a 2% increase in obesity (Basu et al.,
2013b). Critics of the sugar-obesity theory, however, point out the substantial time lag
between changes in sugar consumption and change in obesity rate. After sugar consumption
had begun to decline (Welsh et al., 2011), van Buul et al. (2014, p. 119) noted that “over
the last 5 years, the global annual consumption of carbonated soft drinks has remained
constant or even has declined “Obesity rates, however, seem to have increased
independently of these shifts.” In 2014, for example, obesity rates were still rising,
despite the 25% decrease in added sugar consumption among U.S. residents between 1999 and
2008 (van Buul et al., 2014; Welsh et al., 2011). By 2017, obesity rates had only just
started to level off or decrease, in some but not all U.S. states. The delay is such that
annual adult obesity rates from 2004 to 2013 (Centers for Disease Control & Prevention,
2017b) correlate quite well with annual per capita sugar consumption (U.S. Department of
Agriculture, Economic Research Service, 2019) twelve years before, i.e. from 1992 to 2001
respectively, with r2 = 0.933 among the 100 poorest counties in the U.S. and r2 = 0.908
among the 100 richest counties. Although readily observed, this time lag remains
unexplained. While most population health studies explore the effect of environmental,
nutritional or behavioral factors on obesity levels, few have explicitly explored the
temporal delay between cause and effect. A specific study helps illustrate why we would
expect a substantial delay between increased sugar consumption and national obesity rates.
In a 19-month study controlling for other variables, Ludwig et al. (2001) found that for
each additional SSB consumed per day, BMI in children increased by a mean of 0.24 ± 0.14.
This suggests an increase on the order of about 1.6 per in BMI decade per extra daily SSB.
This “back-of-the-envelope” line of thinking motivates our specific modeling approach.
Here we propose that obesity increase can be explained as the accumulated effect of
childhood exposure to excess sugar calories together with continued consumption. Since
childhood obesity tends to predict obesity in adulthood, the rising obesity rates of
adults the 1990s and 2000s ought to reflect their diets as children of the 1970s and
1980s. In 1990, for example, the 18-year-olds entering the adult CDC dataset would have
been born in or about 1972. Current adult obesity rates would have only just begun to
register a decline in sugar consumption that began in 1998. With a model that can capture
these different dynamics, with per-capita sugar consumption as the single input variable,
we present obesity as the cumulative result of excess sugar consumption since 1970. In
formulating a parsimonious, sugar-driven model, our goal is to replicate three different
aspects of the obesity trends in the U.S.: (a) the overall increase of U.S. adult obesity
since 1970; (b) the profile of obesity by age group for a recent year; and (c) the change
in obesity rates by pre-adult age group since 1990.

<h>MODELS AND METHODS</h>
------------------

As shown in Fig. 2, the model generates a matrix of the 46 calendar years, t, from 1971 to
2016, versus life ages, y, from age 2 through age 75. In each cell of this array, obesity
in year t for age y is calculated as a function of obesity for the same cohort in the
previous year, t − 1, when the cohort was one year younger, age y − 1. The model
replicates the generational time lag through a simple stochastic process of superfluous
sugar calories causing obesity rates to increase over the lifespan of each birth-year
cohort. In this multiplicative process, early excesses are compounded over the long-term,
such that excess sugar consumption in childhood register years later as rising adult
obesity rates. The two parameters, β and α, are adjusted for the model to fit two aspects
of the data: the timeline of increase in average obesity rate, and the profile of age
versus obesity rate. The parameter α is the magnitude of the effect, whereas β reflects
the log odds of non-obese individuals in a cohort becoming obese in the next year, as a
function of their excess daily calories (expressed as fraction of a 2000 calories/day
diet). For example, if α = −8.5 and β = 20, then for each age cohort we expect about 0.05%
more obesity in the next year for every 100 extra daily calories (5% of a 2000 calorie
diet). The logit model is non-linear, so with these same α and β values, but with 300
excess calories per day (15% of a 2000 calorie diet), we would expect an additional 0.4%
of the non-obese portion of the cohort to become obese in the next year. The external
input variable, ρt, is the caloric equivalent of the average excess sugar consumption per
capita in the U.S., expressed for convenience as a fraction of a 2000-calorie diet, for
each year since 1970 (U.S. Department of Agriculture, Economic Research Service, 2019). We
used historical data (Wang and Beydoun, 2002) to approximate the age-obesity profile in
1970, which serves as the initial year of the model. The sugar data, recorded by the USDA
(U.S. Department of Agriculture, Economic Research Service, 2019), are annual estimates of
mean sugar consumed (cal/day) per capita in the U.S. since 1970. The data include four
categories: refined sugar, HFCS, fruit juices and “other” sugars, and here we use the sum
of all four of the categories as our estimate of daily added sugar calories for each year.
To test the model versus change in U.S. obesity prevalence, national level obesity rates
for adults adult (20 and over) in the United States were obtained from the CDC, for
selected years 1988–1994 through 2015–2016 (Centers for Disease Control & Prevention,
2019). Two additional estimates of U.S. adult obesity from the 1970s were added; these are
from the National Health and Nutrition Examination Surveys of 1971–1974 (NHANES I) and
1976–1980 NHANES II (Flegal et al., 2016). For obesity among pre-adult cohorts, we used
data reported by Ogden et al. (Ogden et al., 2014) from 40,780 children and adolescents
between 1988–1994 and 2013–2014.

<h>RESULTS</h>
-------

Using two tunable parameters and the record of mean sugar consumption from 1970 to 2016,
the model replicates the average U.S. obesity increase through calendar years and across
age profiles. Using β = 19.9 and α = −8.5, the model simultaneously replicates, firstly,
the growth in average U.S. adult obesity since 1990 (Fig. 3a). Secondly, using these same
parameters, it simultaneously replicates a typical U.S. state's age-obesity curve for 2015
(Fig. 3b). The only aspect of the age profile not replicated is obesity for ages 75 and
over in 2015 (Fig. 3b), which is the cohort who grew up before the rapid increase in added
sugars in U.S. diets. The model also replicates aspects of the change in obesity rates by
age group. Fig. 4 shows how the same model used in Fig. 3 (β = 19.9, α = −8.5) also yields
similar timelines from 1990 to 2014 for ages 2 to 5, 6 to 11, and 12 to 19. The comparison
in Fig. 4 shows that the model is predicting a decline in obesity rate first among ages 2
to 5 beginning in the late 1990s, then among ages 6–11 beginning in the early 2000s, and
subsequently among teenagers after about 2006. In the model, these decreases in obesity
rates are delayed responses to the decline in excess sugars in the late 1990s. The data,
though noisier, reflect these declines with about the same timing for the two younger age
cohorts, but not the teenagers (Fig. 4). For ages 6 to 11, the actual decline was less
than predicted by the model, and for ages 12 to 19, there was no actual decline at all.

<h>DISCUSSION</h>
----------

Here we have modeled the recent increase of U.S. adult obesity as being driven by added
sugar calories over the lifespan of each birth-year cohort. With annual USDA sugar
consumption figures as the input variable, the two-parameter model simultaneously
replicates three different phenomena: the generational lag between sugar and obesity, the
magnitude of the national rise in obesity, and a recent age-profile of obesity rates. Our
results indicate that excess U.S. sugar consumption is at least sufficient to explain the
timing and magnitude of adult obesity change in the past 30 years, even as other factors
(Gentile and Weir, 2018; Muscogiuri et al., 2018; Smits et al., 2017) could be factored
into future models. In doing so, the model addresses a key critique of the sugar-obesity
hypothesis (van Buul et al., 2014; Soenen and Westerterp-Plantenga, 2007) by introducing
the mechanism to explain the years of delay in cause versus effect. The sugar-obesity
hypothesis is also supported by physiological, historical and economic evidence.
Physiologically, sugar consumption elevates lipid levels in the blood (DiNicolantonio et
al., 2015; Lustig et al., 2015; Grande, 1967; Grande et al., 1965; Kaufmann et al., 1966;
Kuo and Bassett, 1965; Macdonald and Braithwaite, 1964; Teff et al., 2004). Although its
specific role in the obesity epidemic is debated (Rippe, 2013; van Buul et al., 2014),
fructose specifically does not stimulate insulin secretion or the production of the
hormone (leptin) regulating long-term food energy balance, such that this sugar tends not
to satisfy appetite (Bantle et al., 2000; Curry, 1989; Havel, 2005; Luo et al., 2015;
Figlewicz and Benoit, 2009; Stanhope et al., 2009) and affects glucose metabolism, lipid
profile and insulin resistance (Beyer et al., 2005; Bocarsly et al., 2010; Bray et al.,
2004; Johnson et al., 2016; Jürgens et al., 2005; Pereira et al., 2017). Consumed from a
young age, sugar consumption appears to have long-lasting effects, not just habitually but
also physiologically, in ways that could explain a generational delay between U.S. sugar
consumption and subsequent obesity rates. Infant and toddler obesity is correlated with
high-sugar infant foods (Koo et al., 2018) and even fructose in breast milk (Goran et al.,
2017). Sugar consumption during pregnancy leads to increases in recruitment of pre-
adipocytes to adipocytes in utero, such that children are born with an increase in fat
cells that will accumulate more fat during life (Goran et al., 2013). By the mid 1970s,
children 0–2 years old were consuming about 6 grams of added sugar per kg of body weight,
about three times that of adults at the time (Fomon, 1975; Life Sciences Research Office,
1976). From the 1970s to the 1990s, soft drinks were increasingly sweetened with HFCS, an
inexpensive, domestically produced liquid sweetener (Corn Refiners Association, 2002).
Between 1977 and 2001, sweetened beverage consumption increased by 135% across all age
groups, equivalent to about 278 additional calories per day (Nielsen et al., 2002; Nielsen
and Popkin, 2004). In the 2000s and 2010s, total added sugar intake in the US declined
(Popkin and Hawkes, 2016), and by 2016, obesity rates in some U.S. states were leveling
off. Because 75-year-olds experienced childhood before the large-scale increase of sugar
in processed foods, they may have developed less lifelong preference for added sugars in
foods, but also it may be that they never laid down excess adipose tissue in during
gestation. These explanations, potentially complementary to each other, may be addressed
by detailed research on this elderly age group. The age-stratified obesity data we used
run through 2013–14, and in the future it will be revealing to see whether teenage obesity
has declined since 2014 as the sugar-driven model predicts. It may be that for high school
ages in particular, the effect socioeconomic status on food choice (Campbell et al., 2019)
is obscured by aggregated obesity statistics. Data from the Centers for Disease Control &
Prevention (2018) from 1999 to 2017, for example, suggest that obesity among high
schoolers may have peaked in 2011 and 2013 among Asians and whites, respectively, but that
obesity had continued to increase among blacks and Hispanics. We speculate that poverty is
a driver of sugar consumption (Alvarado, 2016; Hernandez, 2015; Shrewsbury and Wardle,
2012; Anderson, 2012; Datar, 2017; Hughes et al., 2010; Kowaleski-Jones et al., 2017; Mata
et al., 2017; Moreno et al., 2016; Rosinger et al., 2017; Bentley et al., 2018).
Economically, sugar is an inexpensive source of calories, and sweetened beverages have
been a substantial portion of expenditures for low-income households (Garasky et al.,
2016). Childhood obesity decreased after the 2009 changes in the US Special Supplemental
Nutrition Program for Women, Infants, and Children (Daepp et al., 2019; Pan et al., 2019);
we believe cutting the juice allowance by half helps explain why. If our model is correct,
the effect of this 2009 change will follow these children into adulthood. In the future,
our model should be tested against different socioeconomic and demographic subpopulations,
as well as for nations where there exist historical data on sugar consumption and obesity
rates. For example, our delayed-effect model could offer a plausible explanation for the
“Australian Paradox” (Barclay and Brand-Miller, 2011), that sugar consumption decreased in
Australia at the same time that obesity increased.

<h>CONCLUSION</h>
----------

In summary, we have modeled the recent increase of U.S. adult obesity rates since the
1990s as a legacy of increased consumption of excess sugars among children of the 1970s
and 1980s. Our model proposes, for each age cohort, that the current obesity rate will be
the obesity rate in the previous year plus a simple function of the mean excess sugar
consumed in the current year. With just these inputs, the model can replicate the timing
and magnitude of the national rise in obesity, as well as the profile of obesity rates by
age group, and the different patterns of change in obesity among children and adolescent
age group, where reduction in obesity registered first among young children in the late
1990s. This supports the perspective that the rise in U.S. adult obesity after 1990 was a
generation-delayed effect of the increase in excess sugar calories consumed among children
of the 1970s and 1980s.


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<ART>Weight perceptions, weight control and income: An analysis using British data
=============================================================================

Authors: David W. Johnston, Grace Lordan
DOI: 10.1016/j.ehb.2013.02.004
Year: 2014  |  Pages: 132-139
ASJC codes: 2001
Keywords: Obesity, Overweight, Weight Control, Weight misperceptions

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

The aim of this paper is to better understand one of the mechanisms underlying the income-obesity relationship so that effective policy interventions can be developed. Our approach involves analysing data on approximately 9000 overweight British adults from between 1997 and 2002. We estimate the effect of income on the probability that an overweight individual correctly recognises their overweight status and the effect of income on the probability that an overweight individual attempts to lose weight. The results suggest that high income individuals are more likely to recognise their unhealthy weight status, and conditional on this correct weight perception, more likely to attempt weight loss. For example, it is estimated that overweight high income males are 15 percentage-points more likely to recognise their overweight status than overweight low income males, and overweight high income males are 10 percentage-points more likely to be trying to lose weight. An implication of these results is that more public education on what constitutes overweight and the dangers associated with being overweight is needed, especially in low income neighbourhoods. © 2013 Published by Elsevier B.V.

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<h>INTRODUCTION AND BACKGROUND</h>
---------------------------

Being overweight or obese is known to be bad for your health, yet the prevalence of
obesity is increasing worldwide (Lobstein and Jackson Leach, 2007). Coined as the “most
prevalent nutritional problem in the world” (Lau et al., 2007), the epidemic is most
prevalent in developed countries. For example, in Canada, U.S., France and Australia, 23%
(Linder et al., 2010), 33% (Dorsey et al., 2009), 17% (International Obesity Task Force,
2011) and 25% (International Obesity Task Force, 2011) of the population are classified as
obese (BMI of 30 kilograms per squared metre or greater “for obese (inclusive of 30)),
respectively. While obesity rates are similar for males and females, there is a divergence
between genders with respect to being overweight. For example, in Canada 42.8% of males
and 23.7% of females are overweight (body mass index (BMI) of 25 kilograms per squared
metre or greater” (inclusive of 25)) or obese. The equivalent figures for the U.S., France
and Australia are 40.1% and 28.6%, 41.0% and 23.8%, and 42.1% and 30.9%, respectively
(International Obesity Task Force, 2011). In England, over 40% of men and 30% of women are
overweight or obese (International Obesity Task Force, 2011), with predictions that
without action, 60% of men, 50% of women and 25% of children will be obese or obese by
2050 (Butland et al., 2007). Action is being taken, however, with £75 million of public
health funds and £200 million of external funds earmarked for a public health campaign
called ‘Change4Life’ in 2009 (The Lancet, 2009). This campaign was launched in response to
the extraordinary economic costs associated with the overweight population – approximately
£7 billion per year in England (National Institute of Health and Clinical Excellence,
2006). These estimates include medical costs; being overweight is associated with an
increased risk of type 2 diabetes, heart disease, stroke, high blood pressure, certain
cancers (colon, breast, endometrial and gallbladder), and high cholesterol. However, the
campaign as yet has not produced any visible signals that it is defeating the obesity
epidemic. Therefore, given that the obesity epidemic is not waning either in England or in
other developed countries, there is scope to investigate further its underlying causes. In
this paper, we investigate the obesity-income gradient by estimating the impact of income
on weight perception and weight control in a sample of overweight British adults. While
those of high income may have a lower weight because they can afford a healthier
lifestyle, it is also plausible that they have a more narrowly defined standard for
acceptable body size and adjust their behaviour accordingly. This would suggest an income
gradient with respect to weight perceptions and a subsequent role for weight perceptions
in determining a person's propensity to pursue weight control. An independent income
gradient–weight control relationship is also likely to exist owing to the higher
opportunity costs associated with weight control for poorer people. Our work is related to
two main strands of the obesity literature. The first of these is the literature that
attempts to estimate the impact of income on the propensity to be overweight or obese. So
far, many studies have found that higher socioeconomic status is related to a lower risk
of obesity (Costa-Font et al., 2008; Wamala et al., 1997; Zhang and Wang, 2007). However,
the endogeneity of income in a weight regression complicates these studies interpretation.
That is, income may cause a person to be overweight, being overweight may cause lower
income or common factors may affect both income and overweight status. These factors
include individual heterogeneity such as self-discipline and impulsivity (Cutler et al.,
2003), along with weight misperceptions, which we explore in this work. Attempts have been
made to establish a causal relationship between BMI and income with mixed results. For
example, Quintana-Domeque (2005) utilise the European Community Household Panel (ECHP),
and exploit exogenous variation in household income owing to inheritance, gifts, or
lottery winnings of €2000 or more to instrument for income in an obesity regression. They
explore this relationship for nine countries and find a relationship between income and
obesity only for women in both Denmark and Italy, and men in Finland. Notably, this work
suffers from a weak instrument problem. In the U.S. context, Cawley et al. (2008) exploit
exogenous variation in the social security policy but are unable to identify any
statistically significant relationship between additional social security income and BMI
in the elderly. Schmeiser (2009) examine the effect of family income changes on BMI and
obesity using data from the National Longitudinal Survey of Youth 1979 cohort. They find
that income significantly raises the BMI and probability of being obese for women only.
Finally, using a longitudinal Swedish panel Ljungvall and Gerdtham (2010) estimate the
impact of mean income, positive deviation from mean income and negative deviation from
mean income on weight status using questionable instruments. They find income to be
negatively related to obesity in general. The second strand of literature that our work
relates to concerns itself with the relationship between actual body size and body size
perception. Self-perception of body size is a factor that can influence whether weight
loss is a concern. Clearly, if a person is unaware they are overweight they cannot fully
internalise the costs associated with the health risks of their weight status. This is in
line with research suggesting accurately perceiving oneself as overweight or obese results
in a greater motivation to engage in healthy lifestyle behaviours (Baranowski et al., 2003
and Rhee et al., 2005). Given that misperceptions of a normal weight among the overweight
and obese have been highlighted in the general literature (Collins et al., 1987; Kuchler
and Variyam, 2003; Maximova et al., 2008; Paeratakul et al., 2002; Viner et al., 2006) as
well as in the literature specific to the UK (Wardle, 2002; Johnson et al., 2008) the
problem of a failure to internalise is one that may contribute to the obesity epidemic.
This work aims to explore the role of an income gradient on weight perceptions.
Specifically we focus on individuals who are the targets of obesity campaigns in England.
That is, we focus on the overweight and obese. The potential for income to be associated
with weight perceptions is linked to it being usual for poor individuals to have poor
friends (Tigges et al., 1998; Wacquant and Wilson, 1989) and the likelihood that poorer
people are more likely to be overweight or obese. Therefore, peer effects may imply an
increased propensity for poorer people to perceive being overweight as a ‘healthy’ weight,
which may reflect ideals of body weight among that group (Kemper et al., 1994). This
arises because people's behaviour is likely to be influenced by the norms in their social
environment. Thus, when overweight becomes the norm within a peer group, it is likely that
the negative social stigma associated with being overweight is reduced. The idea that your
social circle can affect your weight is supported by recent research. Christakis and
Fowler (2007) find that weight gain spreads through a population like a contagious disease
owed to individuals being influenced by their friends and relatives; though, Cohen-Cole
and Fletcher (2008) re-estimate these effects and find them greatly reduced and not
significant once a more thorough econometric methodology is utilised. Elsewhere, Maximova
et al. (2008) have shown that young people's perceptions of weight is dependent on the
weight of their parents and friends. Similarly, Blanchflower et al. (2008) describe a
‘keeping up with the Jones weight effect’ where weight perceptions and dieting are
influenced by the individuals that surround us. Overall they suggest that individuals have
different comparison groups, with the highly educated holding themselves to a ‘thinner’
standard. Oswald and Powdthavee (2007) argue that people have a utility function defined
on relative weight and hence choose their weight with reference to the weight of their
peers. Given the higher rates of obesity amongst the poor, this peer effect is likely to
create an income gradient in weight perception and weight control, which further
reinforces the obesity-income gradient. In addition, weight misperceptions among people of
lower income may be explained by lower levels of health knowledge. Alternatively, those
with higher levels of education may simply be more capable of processing health
information available to them about the type of behaviours that yield them good health
(Gottfredson and Deary, 2004).1 Thus far the role of the income gradient on misperceptions
is under explored, however, Wardle and Griffith (2001) have examined the effects of
socioeconomic status – defined as occupational social class. They find using a sample of
British adults that higher SES people have higher levels of perceived overweight, more
closely monitor their weight, and are more likely to state they are trying to lose weight.
Understanding weight misperceptions is important given that those who are satisfied with
being overweight are less likely to do anything about it. Conversely, those who are aware
that they have an elevated BMI are more likely to take action. It is noteworthy that
feeling overweight does not in itself motivate attempts at weight loss, however the
majority of those who feel this way do try to lose weight (approximately 60%) according to
some received studies (Horm and Anderson, 1993; Wardle and Johnson, 2002) and the
literature generally points to a positive correlation between self perceived weight status
and weight control (Crawford and Campbell, 1999, Forman et al., 1986 and Riley et al.,
1998). Even once weight misperceptions are accounted for, given the higher opportunity
cost of weight control for those of lower income it is likely that an independent income-
weight control relationship will exist. For example, this greater opportunity cost arises
because the neighbourhoods in which poorer people live have characteristics that are
positively correlated with obesity such as poor walkability (Sallis et al., 2009), a lack
of healthy food options (Zick et al., 2009), a higher presence of unhealthy food outlets
(Harrison et al., 2011) and greater disorder (Burdette and Hill, 2008). Additionally, the
literature has identified a relationship between income and healthy lifestyle choices
including the propensity to exercise and eat well (Pampel et al., 2010) and higher rates
of dieting (French et al., 1994; Jeffrey and French, 1996).

<h>DATA AND METHODOLOGY</h>
--------------------

Our data source is the annual Health Survey for England (HSE), which is a household level
survey that collects information through an interview, self-completion questionnaire and
medical examination. We pool data from the 1997, 1998 and 2002 surveys and consider prime
working age (25–60) respondents who, according to BMI measurements collected by a nurse,
are of an unhealthy weight: defined either by BMI ≥ 25 or BMI ≥ 30. The individuals are
unaware that they have been classified as ‘overweight’. The survey year, age and BMI ≥ 25
restrictions, as well as a restriction of non-missing income information, leaves us with
an estimation sample of 9089. Data from 1997, 1998 and 2002 are used because in these
years adult respondents were asked questions regarding their weight perceptions and weight
goals. Specifically, individuals were asked: Given your age and height, would you say that
you are: about the right weight, too heavy or too light? At the present time are you
trying to lose weight, tying to gain weight or are you not trying to change your weight?
The responses are used to define two binary variables. The first represents weight
perception and equals one if the individual believes they are too heavy. Given that only
those who are classified as overweight (or obese) are included, this variable also
measures weight misperceptions. The second key variable represents weight control, and
equals one if the overweight (or obese) individual is trying to lose weight. Approximately
75% of overweight (BMI ≥ 25) respondents feel too heavy and approximately 60% are trying
to lose weight (equivalent percentages for the obese sample are 95% and 73%). In other
words, 25% of respondents incorrectly perceive themselves as the right weight, and 40% are
not trying to change their weight (very few overweight respondents feel they are “too
light” or are “trying to gain weight”). However, these sample averages mask heterogeneity.
For example, mean values of weight perception and control are 64% and 47% for men, and 87%
and 75% for women. This suggests that women are more likely to recognise their overweight
status and more concerned with their weight. Similarly, the raw propensities depend upon
income; high income respondents are more likely to recognise their overweight status. Our
empirical strategy is to sequentially estimate richer variants of Eqs. (1) and (2) in
order to test whether the income effect can be ‘explained’ by mediating variables. The
purpose of this exercise is to gauge which covariates are the potential pathways between
income and our outcome (weight misperception/weight control). First we add a set of
baseline controls, which represent demographic information that is personal to the
individual. Therefore, model (1) includes gender, age, age-squared, married, divorced,
number of children, black Caribbean or African, Asian, year 1997 and year 1998. Second,
given the link between obesity and environment our second set of variables (model (2))
pertains to area of residence information: rural versus metropolitan and North-East,
North-West, Yorkshire, West-Midlands, East-Midlands, South-East, and South-West. Next,
model (3) adds general health indicators: long-standing illness and limiting long-standing
illness. Given that income is essentially one dimension of socio-economic status that is
correlated with other dimensions, our next step is to add some of these dimensions.
Therefore, model (4) adds highest educational attainment and employment status: degree,
vocational qualification, A levels, O levels, and employed. In the context of this data,
those who have O and A levels stay in secondary education until the ages of 16 and 18
respectively. Finally, model (5) adds occupation categories: professional, associate
professional and technical, administrative and secretarial, skilled trades, personal
service, sales and customer service, plant and machine operatives, and elementary.2
Importantly, all sets of control variables (1–5) include BMI since it is a significant
predictor of weight perceptions and weight control even amongst samples of overweight and
obese respondents. Note that if we did not control for BMI the estimated income
coefficient would be downward biased – BMI is negatively correlated with income and
positively correlated with our dependent variables.3 Table 1 includes descriptive
statistics for some of the included covariates. Given Eqs. (1) and (2) are estimated using
a non-random subset of the population, the income coefficients may suffer from sample
selection bias. The direction of any bias is likely to be negative because the negative
income–obesity relationship implies that high individuals in the sample (i.e. overweight)
care relatively little about their weight. Therefore, the true income effects are likely
to be larger. To test this proposition we estimated probit sample selection models and
found that the estimated income effects were indeed larger than those from our probit
regression models. However, these models were identified solely through the assumption of
jointly normal disturbance terms, as our data does not contain a defendable exclusion
restriction. For this reason we prefer estimates from probit regression models.

<h>RESULTS</h>
-------

The upper panel in Table 2 presents estimates from the weight perception probit
regressions for overweight samples (BMI ≥ 25), and the lower panel presents estimates for
obese samples (BMI ≥ 30). The reported standard errors are clustered at the household
level are reported to allow for correlation between weight perceptions and weight control
of individuals living in the same household. The figures represent the percentage-point
change in the probability of feeling too heavy for a 1 unit change in log income (i.e.
marginal effects). Note that moving from the 5th percentile to the 95th percentile of the
income distribution (i.e. from impoverished to wealthy) has the effect of increasing log
income by roughly 2.5. Thus, the first estimate in column 1 – 0.046 – implies that moving
from a low to a high income increases the probability of (correctly) feeling too heavy by
around 12 percentage points. The equivalent effect for overweight men is roughly 15
percentage-points (relative to a sample mean of 64%, equalling a 23% increase). Three key
findings are gained from Table 2. First, regardless of the sample – male, female,
overweight or obese – high income respondents are significantly more likely than low
income respondents to recognise they are ‘too heavy’. Second, income effects are larger
for men than women: using the baseline set of control variables, the male effect is
roughly 2 times larger than the female effect in both the overweight and obese samples. A
potential explanation is that low income men are more likely to view larger body size as
an indicator of prowess and dominance than high income men, thus creating an income effect
in body size perception (McLaren and Kuh, 2004. Third, controlling for the respondent's
area and their health has little effect on the income estimates. One potential explanation
for significant income effects is that low income regions tend to have insufficient health
services, and therefore, residents of these regions receive less information regarding the
thresholds for overweight and its dangers. However, the similarity of the estimates in
rows (1) and (2) suggest that this is not the case. It appears that part of the income
effect – but not all – can be explained by higher income individuals having greater
education and working in different occupation types. For example, the income effect for
overweight males drops from 0.066 in model (3), to 0.044 in model (4) with education
controls, and then to 0.028 in model (5) with occupation controls. Having a university
degree is estimated in model (4) to increase correct weight perception (relative to no
qualifications) by 5.2 percentage-points, while having a managerial level occupation is
estimated in model (5) to increase correct weight perception (relative to an unskilled,
elementary occupation) by 8.4 percentage-points. An alternative estimation approach, which
can aid interpretation, is to replace the continuous log income with income categorical
variables. If we take this approach and include dummy variables indicating the quintile of
the income distribution, we find that individuals in the top quintile (richest 20%) are 8
percentage points more likely to feel too heavy than individuals in the bottom quintile
(poorest 20%) – estimated results available upon request. Equivalent effects for the
female and male samples are 5 percentage points and 11percentage points, respectively. We
have also considered whether there exists nonlinear relationships between log income and
misperceptions, but all higher order polynomial terms were insignificant for all
subsamples and covariate sets used in the analysis.4 Our overall interpretation of the
results in Table 2 is that income is an important predictor of weight perceptions given
that income remains a significant predictor of perceptions even after controlling for a
very large set of covariates that are correlated with income. Importantly, this result is
not being driven by all high income people, regardless of their weight status, feeling fat
– perhaps driven by a propensity to seek some idealised body image. We also examined
whether income increases the propensity for an individual who is of normal weight to
incorrectly perceive themselves as overweight. In this regression the estimate of the log
of income is not significant (p = 0.472). Thus it appears that the mechanism is truly that
income promotes correct self-assessment. Table 3 presents similar estimated income effects
from the weight control models. We again find income to be a significant determinant of
whether an individual is trying to lose weight. Importantly, these models are estimated
with only those respondents who feel too heavy, and thus, income is having an effect on
weight control even after controlling for the effect of income on weight perceptions. We
again find the income effect is larger for men, at least in the overweight sample. For
example, in the model that controls for demographics, area of residence, illness,
education, employment and occupation, it is estimated that a rich overweight male is 12
percentage-points more likely than a poor overweight male to be trying to lose weight.
Unlike the weight perception results in Table 2, occupation and education do not appear to
be modifying the relationship between income and weight control.5 Finally, we investigate
whether the income relationships in Tables 2 and 3 hold equally for younger (<40) and
older (≥40) sub-samples. The estimates in Table 4 are from probit models estimated with
the baseline set of controls and samples of overweight respondents. They suggest that the
effect of income on the probability of correctly perceiving yourself as ‘too heavy’ is
larger for older respondents. For example, the effect for older female respondents is
twice as large as the effect for younger female respondents (0.039 versus 0.020), while
the difference between older and younger male respondents is 2 percentage-points (0.066
versus 0.046). In contrast, the estimation results from the weight control models suggest
that the estimated income effect does not differ by age.

<h>DISCUSSION</h>
----------

This work investigates explanations for the strong relationship between SES and obesity
using a large survey of overweight British adults. The aim is to better understand why the
poor are more likely to have elevated BMIs, so that effective policy interventions can be
developed. Our work finds that overweight low income individuals are more likely to
incorrectly believe they are a healthy weight, and conditional on weight misperceptions,
less likely to attempt weight loss. Both of these effects are larger for males than
females. Further research is required to order to tease out the differences in these
gender effects and establish casual effects. A suggestion is that they may be driven by
peer group effects, whereby males’ peer group composition is more sensitive to income than
females. Our two main findings feed into very different policy options. Firstly, for those
who incorrectly believe they are a healthy weight, further research is needed to
investigate the underlying drivers. People often rely on comparison with peers to make
assessments of their weight status, rather than relying upon medical advice. Given that
obesity has become the norm within low income groups, the existence of such effects
implies that people with lower incomes tend to be less concerned with being overweight,
reinforcing the obesity–income relationship. This problem may arise because of mixed
messages in the media concerning optimal body weight size. Deciphering these mixed
messages is more likely to be achieved by those of higher socioeconomic status. The
implication of this reasoning is that more public education on what constitutes overweight
and the dangers associated with being overweight may be needed, especially in low income
neighbourhoods. This is however not the end of the story, as our results also highlight
that there are many who realise they are overweight but are not attempting weight loss.
Again, the cause for this may lie with peer effects models. That is, within a peer group,
friends may realise they are overweight but reinforce bad eating and exercise habits.
Therefore whilst it is not that peer group effects cause the SES/obesity gradient per se,
they do contribute to the growing disparity once a threshold number of individuals with
low SES are overweight. Furthermore, it may be more difficult for those of lower socio-
economic status to lose weight given that their home environment often lacks the necessary
inputs such as an availability of healthy foods and exercise opportunities. The latter
extends from lack of gyms through to safe areas for walking. To remedy such environmental
level factors would involve policy changes that go beyond health-specific policies. It
should be noted that some commentators argue that any policy to address the obesity
epidemic is paternalistic and should be avoided. That is, we should not intervene as
individuals rationally choose their own weight (by consuming and expending a certain
number of calories). It is unlikely that individuals can weigh up the costs and benefits,
both future and present, of this choice. It is also unlikely that the overweight weigh up
the costs that fall on the health service owing to the obesity epidemic. As discussed,
these costs are expected to rise to £10 billion per year by 2050 with no government action
(Butland et al., 2007). Equally they are unlikely to consider the wider costs to society
and business, such as decreased tax revenue and loss of productivity due to related
illnesses, which are estimated to reach £49.9 billion per year (2007 prices) if the
obesity epidemic is allowed to continue its current increasing trend (Butland et al.,
2007). Therefore, we argue that policy makers must take some action, and from our work,
additional education on what constitutes a healthy weight and adopting a healthy life
style for low income households could be beneficial, without being regressive given that
our work highlights that income is a strong predictor of weight misperceptions and
control. Perhaps these could be piloted in a subset of low income neighbourhoods initially
so cost effectiveness can be gauged. A bigger challenge lies with addressing the
environmental factors that may inhibit individuals losing weight. While the literature has
done well in highlighting that various environmental factors do indeed influence a
person's health status, the next challenge is to identify the main factors that could do
the ‘heavy lifting’ with respect to addressing the obesity epidemic.


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<ART>What doesn't kill you makes you poorer: Adult wages and early-life mortality in India
================================================================================

Authors: Nicholas Lawson, Dean Spears
DOI: 10.1016/j.ehb.2015.11.006
Year: 2016  |  Pages: 1-16
ASJC codes: 2001
Keywords: Disease environment, Early-life health, India, Infant mortality, Wages

--------------------------------------------------------------------------------

<h>ABSTRACT</h>
--------

A growing literature indicates that effects of early-life health on adult economic outcomes could be substantial in developing countries, but the magnitude of this effect is debated. We document a robust gradient between the early-life mortality environment to which men in India were locally exposed in their district and year of birth and the wages that they earn as adults. A 1 percentage point reduction in infant mortality (or 10 point reduction in IMR) in an infant's district and year of birth is associated with an approximately 2 percent increase in his subsequent adult wages. Consistent with theories and evidence in the literature, we find that the level of schooling chosen for a child does not mediate this association. Because of its consequences for subsequent wages, early-life health could also have considerable fiscal externalities; if so, public health investments could come at very low net present cost.

--------------------------------------------------------------------------------


<h>INTRODUCTION</h>
------------

A growing literature documents that workers exposed to better early-life health and less
disease in early life have higher human capital as adults. Although this literature has
largely focused on developed countries, economists have hypothesized that an effect of
early-life health and disease externalities could be importantly larger in developing
countries, where disease insults are worse and more varied (Currie and Vogl, 2013; Spears,
2012b). If early-life health indeed importantly limits human capital in developing
countries, wages could be a mechanism through which health has important effects on
developing economies and, because of income and consumption tax revenue, on the
government's budget. However, the magnitude of these effects is a topic of current debate
in the development economics literature (Acemoglu and Johnson, 2007; Bleakley, 2010a;
Hansen, 2014). It is therefore important to understand and quantify relationships between
early-life health and subsequent wages in developing countries (Vogl, 2014). Our article
documents a robust gradient between the health environment to which today's workers in
India were exposed as infants in past decades, and the wages which they now earn. We match
male workers in nationally representative survey data on wages in 2005 to district-level
estimates of infant mortality in their year of birth, which we use as a measure of early-
life health and disease, following Acemoglu and Johnson's investigation of mortality and
GDP. We then use a double fixed effects (place and time) identification strategy to
compare workers in the same district labour market today who were exposed to different
mortality regimes when they were born. Our results suggest that being born in a district-
year with a higher infant mortality rate (IMR) – and corresponding worse health and
disease environment – is associated with a significant but plausible reduction in earnings
decades later. A 1 percentage point reduction in infant death (or a 10 point reduction in
IMR) in the environment to which an infant was exposed in his year of birth is associated
with an approximately 2 percent increase in his subsequent wages as an adult. Because
important threats to early life health remain widespread in India and other developing
countries, these estimates are of continuing economic and policy importance. Bleakley
(2010a) reviews theory and evidence that disease – and especially child health – could
have important effects on adult human capital and income in developing countries. Although
substantial effects would be consistent with current theory and recent empirical findings,
there is debate about the quantitative importance of disease to economic development.
Bleakley further presents a model demonstrating that improved early-life health is likely
to increase both the returns to schooling and the opportunity costs of schooling (in the
form of higher earning ability for children and young adults); as a result, improvements
in early-life health may not lead to large increases in the optimally-chosen quantity of
formal schooling. Our setting allows us to test this prediction, and indeed we find links
between improvements in early-life mortality and adult wages, but no association between
IMR and subsequent schooling. Infectious disease is well-known to have negative
externalities on neighbors. Because of its consequences for subsequent wages, the disease
environment also can have fiscal externalities, which are of importance for government
cost-benefit analysis in the context of a developing country with limited fiscal capacity
and many competing potential expenditures. We apply our estimates to compute considerable
consequences for government tax revenues of reductions in income and consumption due to
early-life health and disease. We show that relatively modest effects of early-life health
on individual economic outcomes can add up to quantitatively important overall economic
and fiscal effects, in the context of a developing country with a large burden of disease
externalities. One consequence is that public action to improve the disease environment
faced by infants could come at very low net present cost to governments (Alderman and
Behrman, 2006). The rest of the article proceeds as follows. Section 2 provides a brief
overview of relevant literatures and the Indian context, and Section 3 details our
empirical strategy. Section 4 then presents our main empirical results, and Section 5
demonstrates the robustness of our results in several directions and explores the
mechanisms driving our findings. Section 6 translates the main empirical results into
implied consequences for government revenues and a simple measure of welfare. Section 7
concludes.

<h>BACKGROUND</h>
----------

We study adult male workers in a representative survey of India. Children in India today
are exposed to a considerable disease burden in early life, which was even greater at the
time when today's adults were children. In 1970 – the year before our data begins, when 35
year old workers in 2005 were born – nearly 20 percent of children died before their fifth
birthday, and 13 percent of infants died in their first year of life (Unicef, 2012).
Infant mortality in India has fallen to about 4.1 percent today, but this still
substantially exceeds infant mortality of 1.1 percent in China and 3.3 percent in
Bangladesh, a poorer neighboring country. If early-life health and disease is an important
constraint on development and income, it would be of considerable importance in India,
where about one-fifth of all births occur.

<hs>  Effects of early-life health on adult economic circumstance</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

An active literature in economics documents that healthier babies are more likely to
become healthier and more productive children and adults (Currie, 2009). Early-life health
matters because the first few years are a critical developmental period; children who have
better health and net nutrition in early life are more likely to reach their physical
growth potentials and are more likely to reach their cognitive potentials (Case and
Paxson, 2008). Indeed, much of this literature, unable to match adult wages to early-life
conditions, has used adult height as a proxy for early-life health (e.g. Vogl, 2014). Most
of this literature has focused on developed countries (e.g. Deaton and Arora, 2009).
However, the impact of early-life health in developing countries may be an even more
important part of labour market outcomes than in developed countries, relative to
heterogeneity in genetic potentials: disease conditions are worse, care and remediation
may be less available, and heterogeneity in health insults is likely to be larger than in
developed countries. Economists have linked various measures in the chain from early-life
human capital accumulation to its long-run consequences: childhood and adult height,
childhood and adult cognitive achievement, and adult wages. For example, Bozzoli et al.
(2009) show that people are shorter in countries with higher infant mortality, whereas de
Oliveira and Quintana-Domeque (2014) find that GDP per capita in year of birth is the main
correlate of height in late-20th-century Brazil; Alderman et al. (2009), Alderman et al.
(2006), and Glewwe et al. (2001) show that taller children have greater cognitive
achievement; Vogl (2014) shows that taller adults in Mexico earn more money; and many
papers in labour and development economics document economic returns to cognitive
achievement. Among the few studies that have been able to directly connect variations in
disease environment to gains in wages or consumption are two recent papers by Bleakley
(2010b) and Cutler et al. (2010), who estimate effects of early-life exposure to malaria
on adult wages in the Americas and on consumption in India, respectively.2 Our article
expands this literature beyond malaria and links the early-life mortality environment
directly to adult wages in a developing country; we then apply our estimates to compute
consequences for government revenue, in the context of a large developing economy where
our estimates are of continuing relevance.

<hs>  Endogenous education and the envelope theorem</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

It is common in the literature linking early-life health to adult wages to verify an
intermediate effect on schooling (e.g. Vogl, 2014). Bleakley (2010a) presents a standard
model in which children's education is optimally chosen to maximize lifetime income. The
benefits and costs of education both depend on the child's health, and therefore on the
disease environment. Bleakley notes that better health almost certainly increases the
returns to schooling, but better health is quite likely to also increase the opportunity
cost of schooling in an economy where children can also engage in productive work, as
would have been common in India several decades ago. Therefore, it is not clear that the
effect of health on education should be positive. Moreover, Bleakley (2010a) shows that a
straightforward implication of the envelope theorem is that the chosen schooling level is
unlikely to be an important mechanism of the effect of health on adult earnings: if
schooling is chosen to maximize lifetime income, for example, individuals will attain
schooling up to the point at which the marginal gain from schooling in terms of added
lifetime earnings (accounting for foregone earnings while in school) is zero. Therefore,
even if changes in early-life health impact cognitive development in such a way as to
increase the quantity of schooling chosen, this change in schooling should have no first-
order impact on lifetime earnings; rather, any effect of early-life health on adult
earnings should primarily accrue through improvements in human capital independent of the
level of schooling. Because we observe an adult's early-life mortality environment, his
wages, and his level of schooling, we are able to test these two theoretical predictions.
We find that exposure to better early-life health is indeed associated with earning higher
adult wages. However, we find no similar association with education levels, and flexibly
controlling for a detailed education vector does not influence the magnitude of the
gradient we document between early-life health and adult earnings, as predicted by
Bleakley (2010a).

<h>EMPIRICAL STRATEGY AND DATA</h>
---------------------------

In this section, we outline a strategy to quantify the gradient between the early-life
mortality environment and adult wages. Although we write about “identification,” we do not
interpret our results literally as an effect of early-life mortality outcomes on wages;
rather, adult economic outcomes and infant mortality are both shaped by an early life
health and disease environment, which includes sanitation and other dimensions of public
health. We use a double fixed effects (place and time) identification strategy to compare
workers who compete with one another within the same labour market today, but were exposed
to better or worse disease environments and mortality regimes when they were born. Our
identification strategy exploits two facts about a cross-section of workers of different
ages who live near one another: First, their wages today are determined, in part, by a
common labour market. Insofar as labour is substitutable across workers of different ages,
those workers are offering to supply their labour to the same, shared demand side of the
market.3 Second, workers of different age cohorts in a cross-section implicitly form a
synthetic panel: workers of different ages today represent the effects of early-life
health at the different points in history when they were born. We exploit district-by-time
variation to investigate the association between adult wages in 2005 and early-life health
in districts throughout India in the 1970s and 1980s. In particular, we match historical,
district-level census data on early-life mortality with cross-sectional survey data on
adult wages. Fig. 1 presents our identification strategy graphically. The graph plots
average wages, net of district fixed effects, as a linear function of age. The most
visible feature of the graph is the upward slope: within essentially all Indian districts,
older workers are paid more than younger workers, on average. Our identification is found
in the difference between the two slopes. Early-life health improved over time in
essentially all districts. However, these improvements were not uniform across districts.
In districts where the mortality environment improved more quickly over this period,
younger workers would be expected to have relatively better early-life human capital than
older workers in the same district, in comparison with the difference between older and
younger workers in other districts where the health environment improved more slowly.
Therefore, our identification strategy asks whether the positive gradient between ages and
wages is less steep in districts where the mortality environment improved more quickly. An
initial answer is visible in the difference in the two slopes in Fig. 1: the age profile
of wages is less steep in the half of districts with above-average declines in infant
mortality.

<hs>  Sources of historical and contemporary data</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We match data from two different sources. For our present-day dependent variables and
control variables, we use data on individual adult males from the India Human Development
Survey (IHDS), a nationally representative 2005 cross-sectional survey of 40,000
households (Desai et al., 2007). We study men born between 1971 and 1989, who were
therefore between 16 and 34 years of age in 2005, leaving us with 12,783 observations, as
can be seen in Table 1. These observations are drawn from 277 districts across 17 states,
including the 13 most-populated states as of the 2011 Census which comprise over 85% of
the total population; the full list of states covered by our data can be found in Online
Appendix B.2.4 Our primary dependent variable is the log of hourly wages in rupees, as
computed by the IHDS.5 As a robustness check and an input to our welfare computations, we
also estimate the gradient between the early-life mortality environment and household
consumption per capita. For our independent variable, we use historical infant mortality
rates, a standard variable in the economic history and economic demography literatures.
Infant mortality rates (IMR) are scaled as the number of deaths in the first year of life
per 1,000 live births. Economic historians have long used infant mortality as a measure of
the disease environment. Because of consequences of disease for net nutrition, early-life
infant mortality rates are increasingly well understood to be an important determinant of
height in developing countries today (Bozzoli et al., 2009), and historically in now-rich
European countries (Hatton, 2014).6 Of course, we do not literally estimate effects of
infant mortality: we would not expect average wages in a district to rise as a result of
an emergency medical intervention that barely prevented the deaths of the marginally last
infants to die. Instead, we interpret the gradient that we document between mortality and
subsequent wages to reflect the influences of the health and disease environment on both.
In the 1970s and 1980s, infant mortality would have been importantly shaped by infectious
disease and maternal nutrition, rather than by perinatal medical care; the first recorded
data on the percent of births attended by any skilled medical staff in the World Bank
World Development Indicators is 34.2 percent in 1993. We match district-level historical
IMR data from various rounds of the Census of India to the IHDS. Census data is available
only at 10 year intervals, specifically in 1981, 1991 and 2001; such ten-year intercensal
periods are standard in demographic data, and infant mortality data at the district level
does not exist for any Census prior to 1981. We use these three Census rounds to estimate
a long difference in IMR by district: we run a district-specific linear regression of
census IMR on year for each district, and use regression coefficients to predict IMR for
each year from 1971 to 1989, thus matching the adults we study with the predicted IMR in
their district, in the year of their birth. Results are robust to the alternative use of
log-linear regressions, or instrumenting for the linearly-predicted IMR with the log-
linear prediction to deal with potential measurement error in infant mortality, as we will
show.7 Given the 10-year interval between each Census round, we do not project IMR
estimates any further into the past than 10 years prior to the 1981 Census, which
determines the start date of our data as 1971. This procedure provides the best possible
estimates of infant mortality rates by district over the 1971–89 period, but our estimates
are not sensitive to the start date; a robustness check in Online Appendix D shows that
our point estimate is numerically very similar – and even slightly larger in absolute
value – if we omit all years prior to 1981. In a subsequent robustness and plausibility
check, we use district-level sanitation rates, operationalized as the percent of
households in a district who own a toilet or latrine, rather than defecating in the open.
Early-life exposure to open defecation in India has recently been shown to be a
significant predictor of infant mortality, childhood height (Spears, 2013) and childhood
cognitive achievement (Spears and Lamba, 2016).8 We also take this historical data from
the Indian Census from 1981, 1991 and 2001, where in this case data is available
separately for the urban and rural portions of each district (when a district contains
both). Rural open defecation is not observed in the 1981 Census, but the World Health
Organization estimated that as of 1980, only 1% of India's rural population had access to
any sanitation facilities, so we assign 100% rural open defecation in 1981,9 and predict
sanitation rates for each observation by performing separate district-specific regressions
for rural and urban sections of each district. As a result, we use a smaller, younger
sample in the sanitation robustness check; rural open defecation was almost universal
before 1981, and therefore there is no improvement to be studied. Table 1 presents summary
statistics for the IHDS and census data that we use. Our average workers are poor –
earning about 10 rupees an hour, or about $0.23 in 2004 dollars (roughly $1 at purchasing
price parity) – and were exposed to threatening early-life health environments, with
infant mortality of 113 deaths per 1000 births and only about 17 percent sanitation
coverage, on average. The maximum estimated IMR in our sample is 281, and the minimum is
29.7; the average individual lives in a district in which the IMR declined by 2.8 points
per year, but there is considerable variation in this measure, ranging from a 10 point
reduction per year to a 1.8 point increase. The workers we study are also relatively
young, with an average age of about 26 years.

<hs>  Empirical specification</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~

It is important to note that any coefficient on IMRdt that we observe can only be
consistent with a factor that changed over time within districts in parallel with
improvements in early-life health, and which, in a contemporary cross-section,
differentially impacts people who were born a few years apart; that is, people who would
have been subjected in similar ways to changes in village infrastructure, education, or
cultural norms. Because these wages are observed in a cross-section of workers of
different ages, any difference across local labor markets would be absorbed by district
fixed effects. Our specification thus rules out many forms of spurious correlation driven
by factors other than early-life health. To further demonstrate the robustness of our
strategy, as well as the stability of our coefficient estimate, we add controls Xidt in
stages: state-specific linear time trends: identifies the effect of early-life health from
the extent to which the district time trend in IMR differs from the state-wide time trend,
to rule out any spurious state-level omitted variables; state × urban fixed effects:
controls for a separate rural–urban difference in each state; state × social group
indicators: state-specific indicators for eight caste and religion groups; female
literacy: district-level female literacy in the district and year of the man's birth,
matched from census data in the same way as IMR. The control for female literacy – another
indicator of human development and an important determinant of early-life human capital –
helps ensure that we are identifying off of variation in early-life health and the disease
environment rather than improvements in other district facilities and outcomes, and also
verifies that no spurious correlation is mechanically introduced by our district-level
matching process. We will additionally add a further set of covariates which may entail
overcontrolling, relative to a properly specified model, but which will allow us to
further rule out omitted variable bias while investigating possible mechanisms of the
effect we document. In particular, we will add indicators for the worker's membership in
seven job categories,10 which rules out spurious structural differences in district labor
markets. Finally, we will add detailed indicators for years-of-school interacted with
literacy. These additions would be overcontrolling if education investments were partially
caused by early-life health. However, as we have discussed, models of optimal investment
in education suggest that improvements in early-life health could increase adult wages
without having a large effect on schooling decisions. Moreover, schooling may not be an
important mechanism of the translation of early-life health into adult wages. In a test of
this theoretical prediction, we will show that our empirical strategy finds no effect of
early-life IMR on education, and no impact on our main coefficient of interest when we
include education variables in the regression. Our strategy implicitly assumes that the
young adult men in our sample were born in the same district in which they lived at the
time of our data. This is a reasonable assumption, because permanent migration for adult
males in India is relatively uncommon (Rosenzweig and Stark, 1989); in contrast, women
often migrate at the time of marriage to join their husbands’ households.11 We will
demonstrate that our results are not affected by migration: permanent migration is
observed in the IHDS, and excluding the small fraction of men who have ever moved
residences does not meaningfully change our coefficient estimates.

<h>EMPIRICAL RESULTS</h>
-----------------

Are men who were exposed to a better early-life health environment, as measured by infant
mortality, subsequently paid higher wages as adults? As an initial answer to motivate our
main result, Fig. 2 verifies that men who were born in district-years with worse infant
mortality and sanitation earned lower wages as adults in the IHDS in 2005. Panels A and B
plot locally weighted kernel regressions depicting a clear downward trend. Panels C and D
plot residuals of wages against residuals of our health measures, in both cases after
controlling for year-of-birth and state-times-urban fixed effects, with the means added
back in to make the range of the figures comparable to A and B. The visible downward trend
remains, in an initial suggestion of the gradient we will estimate.

<hs>  Main result: adult wages and early-life mortality rates</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Table 2 presents our main empirical result: men who were born in district-years with
higher infant mortality have lower adult wages, on average. The regression coefficients
imply that a 1 percentage point increase in the infant mortality rate (that is, 10 more
infant deaths per 1000 live births) would be associated with a decline in adult wages of
almost 2 percent.12 The mortality-wage gradient is notably stable across regression
specifications. In particular, similar results are found if IMR is projected linearly
across survey rounds, as in Panel A, or if linear prediction is instrumented for with log-
linear projection, as in Panel B, to reduce measurement error. Adding a long vector of
regression controls fails to importantly change the coefficient estimate. In particular,
column 2 controls for state-specific linear year-of-birth trends (age gradients), separate
urban indicators for each state, and separate religious and caste indicators for each
state; the coefficient remains essentially identical, and if anything slightly increases.
Column 3 goes further by including indicators for job categories, which may well be in
part a consequence of early-life health and human capital accumulation (Vogl, 2014). This
does not change the coefficient on early-life IMR exposure. This suggests that job
categories are not omitted variables that are spuriously responsible for our main result
and that early-life health does not appear to be related to wages through the mechanism of
sorting into these categories.13 Column 4 tests Bleakley's envelope theorem observation:
chosen schooling should not mediate the relationship between early-life health and adult
wages. Controlling flexibly for education, measured as a vector of school-grade indicators
interacted with literacy, has no effect on the coefficient on birth-year infant mortality.
Rather, the link operates through improvements in human capital at the same level of
schooling. Note that this is not merely because the schooling variables are too noisily
measured to have a signal; in the regression of column 4 of panel A, the vector of
education indicators is highly statistically significant with a test statistic of F31,276
= 19.69, p < 0.00001. Finally, column 5 controls for census female literacy rates in the
district and year of the man's birth; although the sample decreases slightly because this
cannot be matched to all district-year combinations, the stability of the coefficient
suggests that the gradient we observe is due to the early-life health environment, rather
than historical human development more broadly.14 A robustness check in Online Appendix D
further demonstrates that our coefficient estimate is stable across different start dates
for our data; in fact, the association between IMR and subsequent wages even becomes a bit
stronger when data on individuals born in the 1970s is discarded. A robustness check in
Online Appendix D further demonstrates that our coefficient estimate is stable across
different start dates for our data; in fact, the association between IMR and subsequent
wages even becomes a bit stronger when data on individuals born in the 1970s is discarded.

<hs>  Bleakley's optimization result: no effect on education</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Improved early-life health could increase adult human capital by increasing physical
strength or cognitive ability directly, or by increasing attained schooling, which would
in turn increase wages. However, Bleakley (2010a) predicts that the optimally chosen
quantity of schooling should not be an important mechanism linking early-life health to
adult wages, and that schooling may not even increase in response to an increase in early-
life health, because health increases both the benefits and costs of a child attending
school. We have seen evidence for the first claim; in Table 3 we test the second. Neither
the early-life environment proxied by IMR nor the level of sanitation (which we will
consider as a robustness and mechanism check in subsequent sections) are associated with a
difference in schooling levels. To emphasize, this is not because the schooling variables
are unreliable noise: they are quite significant predictors of adult wages.

<h>ROBUSTNESS AND MECHANISMS</h>
-------------------------

In this section, we present three further empirical tests of the robustness of our main
result and of the plausibility of a link between the early-life health environment and
adult wages. First, we show that early-life exposure to open defecation – one important
determinant of infant mortality in India – is similarly associated with adult wages. Then,
returning to the concern that we observe only a man's district of residence and not of
birth, we rule out migration as a cause of our result by showing that the result is
similar when migrants are excluded. Finally, we document a similar association between the
early-life health environment and household consumption, but only for households in which
the man we study is the main earner. This will be an input into our welfare calculations,
and is an important plausibility check for the consistency of our result with economic
mechanisms, rather than it reflecting a spurious correlation.

<hs>  Early-life exposure to open defecation</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Among potential health insults, exposure to poor sanitation is particularly likely to have
quantitatively important consequences for adult economic outcomes because its effects on
early-life health are so large. Water and sanitation are known to be important
determinants of health outcomes, especially infant mortality (for recent examples in
economics, see Cutler and Miller, 2005; Galiani et al., 2005; and Watson, 2006).
Nonetheless, the associations between human capital and sanitation and disease have
received relatively less research attention than human capital gradients in income and
education. However, a recently active literature has shown that sanitation can be
particularly important in human capital accumulation in developing countries, especially
in India, where open defecation – without using a toilet or latrine – is particularly
widespread (Spears, 2013). Open defecation matters for health because it releases fecal
germs into the environment which cause disease in growing children. According to Unicef
and WHO (2012) statistics, over a billion people worldwide defecate in the open; most of
these live in India, and most people who live in India defecate in the open. As a large
medical and epidemiological literature documents, ingestion of fecal pathogens as a result
of living near poor sanitation is well-known to cause diarrhea (Esrey et al., 1992).
Checkley et al. (2008) use detailed, high-frequency longitudinal data from five countries
to demonstrate effects of childhood diarrhea on subsequent height. In addition to the
obvious threat of diarrheal disease, open defecation can cause net nutritional insults
through worm or other parasitic infections, or by increased energy consumption fighting
disease. Most recently documented in detail in the medical literature, but perhaps very
important, is the possibility of widespread chronic but subclinical environmental enteric
dysfunction (Humphrey, 2009). Economists have further identified effects of childhood
exposure to sanitation-related disease on human capital (Bleakley, 2007; Baird et al.,
2011). Substituting sanitation coverage for infant mortality as the independent variable
in our regressions allows us to provide further evidence of a link between the early-life
disease environment and adult wages. Open defecation is only one of many important causes
of historical and contemporary infant mortality in India, and as such sanitation and IMR
are far from perfectly negatively correlated: among individuals in our baseline wage
regression for whom both IMR and sanitation data are available, the correlation is −0.196.
In fact, the correlation between the changes in IMR and sanitation that we use for
identification is essentially zero: in fact, it is slightly positive at 0.0637, because
districts that saw the greatest reductions in IMR tended to be the districts with the
worst disease environment, and thus with the highest starting IMR, whereas sanitation in
those districts tended to improve more slowly.15 Therefore, the regressions below make use
of a second, and quite different, source of variation in early-life health environment,
making it less likely that both are simply capturing some other unobserved variable. Thus,
insofar as results using sanitation are broadly similar to results found using IMR, we
interpret this concordance as indicative that the mortality results are plausibly
consequences of the disease and health environment. Table 4 reports regression results
with sanitation coverage as the independent variable. The sample is smaller in Table 4
than in the IMR analysis because we only use data on individuals born in 1981 and after,
as rural open defecation was almost universal before this period, meaning there was no
improvement to study; this smaller sample will decrease the precision of coefficient
estimates. As the table shows, we indeed find a gradient of important but plausible
magnitude between early-life sanitation and adult wages. The main independent variable is
the percent of households owning a toilet or latrine, rather than defecating in the open.
A 10 percentage point decrease in open defecation translates into an approximately 2–3
percent increase in wages. Thus, we find that in districts where sanitation has improved
more quickly over time, the within-district wage profile is less steeply increasing in
age. As before, our result is quantitatively stable as a long vector of controls is added,
including for state-specific time trends, caste and religious groups, and state-specific
urban residence. Also as before, adding job categories and education indicators – although
these are, themselves, predictive of wages – does not change the coefficient on early-life
sanitation.16 Crossing these produces 15 predictions of the coefficient for wages
regressed on early-life sanitation coverage. These range from 0.0006 to 0.0052, with a
median of 0.0017 and a 75th percentile of 0.0021. This is exactly the neighborhood of our
estimates in Table 4: 0.0018–0.0032. Although our estimates are slightly above the median
of these estimates, there is reason to suspect our estimate would be larger: a higher
fraction of the variation in height in India reflects early-life health than in the U.S.
or likely even than in Mexico. Indeed, Spears (2012b) finds that the gradient between
height and cognitive achievement is much steeper for Indian children than for U.S.
children. Therefore, we conclude that our estimates are quantitatively consistent with
predictions from estimates in the literature.

<hs>  Results are not driven by migration</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Because we observe the district in which men live, not the district in which they were
born, certain patterns of endogenous migration could, in principle, bias our estimates.18
Fortunately, the IHDS includes data on migration, so we can assess the importance of this
concern. The data report whether a particular individual moved homes since their birth,
though we cannot see where they migrated from, so we are likely to overstate migration as
many moves would be within the same district. We run the regressions of wages on IMR and
sanitation only for stayers, by omitting all individuals who report ever having moved
(even those who move within districts). The results are presented in Table 5, and the
coefficients are nearly unchanged. Further analysis in Online Appendix C finds no evidence
that selective migration along the dimension of improvements in early-life health occurred
in any case. Therefore, selective migration does not appear to be responsible for our
results.

<hs>  Effects on consumption</hs>
  ~~~~~~~~~~~~~~~~~~~~~~

In this section, we extend our analysis to check for a gradient between early-life
mortality and household consumption per capita. In part, this is a robustness check of our
main results: we would expect an increase in income to increase household consumption,
especially if the adult male we study is an important source of household income.
Additionally, these estimates will be used in our fiscal and welfare computations:
consumption taxes – such as value added tax – are a larger fraction of government revenue
in India than income tax, so if we are concerned about the fiscal impacts of the early-
life health environment, it is important to confirm that consumption is affected as well.
Table 6 documents the association between early-life IMR and the log of household monthly
consumption per capita.19 Column 1 repeats the estimate of the gradient between early-life
IMR and wages from Table 2. Column 2 shows that the association with household consumption
is of similar magnitude, although slightly smaller. Importantly, however, the adult men
whom we are able to study are relatively young, and only some of them will be significant
earners for their households. One common family structure in India is a joint household
where adult men and their spouses live with the man's parents; such households could have
multiple brothers and a father earning income. Column 3 restricts the sample to the
approximately two-thirds of the men we study who earn the most money of all people in
their household; the effect is quantitatively similar to the effect on wages in column 1.
Column 4 presents results for men who are not main earners; their early-life health
environment has no detectable effect on their households’ consumption. This non-finding is
important because it is consistent with what the economic demography of the Indian context
would predict; this therefore suggests that our finding is not merely a spurious
reflection of correlation between some aspect of households’ socioeconomic status today
and the health environment in their districts in past decades.20 For example, our results
are not driven by factors that impact the entire family: if IMR or sanitation in birth
year was simply capturing general improvements in village infrastructure, the impact
should be felt by all earners today, not just those families where the current primary
earner was an infant at the time of the improvement.

<h>FISCAL AND WELFARE IMPLICATIONS</h>
-------------------------------

Our analysis so far has produced coherent evidence that improvements in the mortality
environment are associated with higher subsequent wages and consumption. As a result, we
expect that such improvements would have positive consequences for the tax revenues
collected by the Indian government. Importantly, this suggests that investments in
improved early-life health, such as investments that lead to increased use of improved
sanitation, could come at a low net fiscal cost to the government of a country such as
India. It is also likely that higher income and consumption will translate into increased
welfare for Indian households. However, this is not certain in a context of non-unitary
households; Indian households are often large and complex, and it is beyond the scope of
our analysis to evaluate who receives the increase in consumption within a household, and
how that might affect intra-family relations or bargaining power. The IHDS does not
observe person-level consumption, only household-level. Thus, we can evaluate the impact
of improvements in the early-life disease environment on household consumption, and
aggregate the gains up to an economy-wide level, and for simplicity we will refer to these
as welfare gains; but it should be understood that we do not claim that increases in
household consumption can be monotonically translated into gains in actual person-level
welfare. Our estimated consumption gains could more accurately be interpreted as increases
in potential household well-being, while the actual welfare gains could, in principle, be
larger or smaller than what we estimate. Therefore, in this section, we translate the
empirical estimates from the previous sections into fiscal and welfare terms, to provide
an illustration of the aggregate impact of early-life health on the Indian economy. For
example, if a 1% point reduction in IMR is associated with 1.74% higher wages, we use
details of the Indian tax system to estimate the associated increase in future tax
revenues, as well as the increase in after-tax income and thus consumption. In each case
that we study, the gains in tax revenue and consumption at an aggregate level are large,
at least $10 billion in present-value terms; these results demonstrate that improvements
in early-life health are associated with substantial gains to the government and to the
Indian population. Independent of the accuracy of our main empirical estimates, this
section is important in the context of Acemoglu and Johnson (2007), Bleakley (2010a), and
others for computing what moderate microeconomic relationships of the sort that we
estimate could add up to in a large economy.

<hs>  Fiscal externalities of early-life health</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

We begin with an analysis of the association between early-life mortality environment and
tax revenues, using the result from column 1 of Table 2 as our baseline estimate: a 1%
point increase in IMR is associated with 1.74% lower wages. We then assume that the impact
of IMR on tax revenues is also 1.74%; thus we conservatively assume that the income
elasticity of tax revenue is 1, even though studies of both developed and developing
countries tend to find that increases in income lead to proportionately greater increases
in tax revenues.21 We limit our attention to the income tax and excise and service taxes,
as these are taxes which depend directly or in a close indirect way on income and
consumption; we ignore customs duties as well as the corporate tax, even though one might
expect more productive workers to lead to larger corporate profits. The revenue from these
taxes amounted to about 5.11 trillion rupees in 2012–13, or $93.64 billion US;22 we assume
that a normal working life is 40 years, from 18 to 57, and assume that each year-of-birth
cohort produces an equal share of the tax revenue, or $2.34 billion per cohort, prior the
change in IMR being considered.23 Because these revenue gains occur in the future,
starting when the year-of-birth cohort born today enters the labour market, and gradually
phasing in after that as more “treated” cohorts enter, we can use a 3.81% discount rate24
to add up these future gains and express the revenue gains as a present-value equivalent.
This simple procedure allows us to calculate the expected effect on tax revenues from a 1%
point reduction in IMR starting today and for each of the next 100 years. Reducing IMR by
1% point produces fiscal gains starting 18 years from now when the first treated cohort
enters the labour market, and ending 157 years from now when the final cohort exits the
labour market; the details of the calculations are relegated to Online Appendix E.1, but
simply adding up the revenue gains from each cohort and discounting, we find that the sum
of the revenue increases is equivalent to $11.70 billion in present value terms.25 As a
sensitivity analysis, we have also evaluated the revenue gains for the highest and lowest
estimates in panel A of Table 2, and for a range of values for the discount rate; the
results are displayed in panel A of Fig. 3. The revenue gain depends on both the
association between IMR and wages and the discount rate, but especially on the latter,
ranging from about $6–9 billion with a rate of 5% to as much as $47 billion with a 2%
discount rate. The black dotted line in the figure shows the baseline discount rate of
3.81%. As a further illustration of the potential fiscal gains from investments in
improving early-life health, we also consider the gain in tax revenues associated with a
more specific public health objective: the elimination of open defecation today, using our
estimate of the association between sanitation and adult wages in Table 4. It was
estimated that 53.1% of Indian households defecated in the open in 2011, but that number
had been declining at an average rate of 1.05 percentage points per year over the previous
decade. Therefore, when considering the elimination of open defecation, the appropriate
counterfactual is one in which open defecation continues to decline over time; we assume a
continued decline at the same linear rate, so that absent any intervention open defecation
would be eliminated in about 50 years. Then, using the result from column 1 of Table 4 as
our baseline estimate, where a 1% point increase in sanitation coverage is associated with
0.296% higher wages, we perform a calculation similar to the one above and find a total
present-value revenue gain of $60.48 billion; details can again be found in Online
Appendix E.1. As a further illustration of the potential fiscal gains from investments in
improving early-life health, we also consider the gain in tax revenues associated with a
more specific public health objective: the elimination of open defecation today, using our
estimate of the association between sanitation and adult wages in Table 4. It was
estimated that 53.1% of Indian households defecated in the open in 2011, but that number
had been declining at an average rate of 1.05 percentage points per year over the previous
decade. Therefore, when considering the elimination of open defecation, the appropriate
counterfactual is one in which open defecation continues to decline over time; we assume a
continued decline at the same linear rate, so that absent any intervention open defecation
would be eliminated in about 50 years. Then, using the result from column 1 of Table 4 as
our baseline estimate, where a 1% point increase in sanitation coverage is associated with
0.296% higher wages, we perform a calculation similar to the one above and find a total
present-value revenue gain of $60.48 billion; details can again be found in Online
Appendix E.1. The purpose of these calculations is to illustrate the potential
quantitative economic importance of early-life health. If we take our results literally as
capturing the causal effect of sanitation coverage on wages, then this implies that if
there existed an investment capable of eliminating open defecation today at a cost of
$60.48 billion or less, there would be no net cost to the Indian government, as those
expenditures would be made up in future tax revenues, even after those future gains were
discounted at a 3.81% rate. To provide an estimate of the revenue gain per unit of
investment (households induced to use latrines), we divide this total by the number of
households currently estimated to defecate in the open, which is approximately 131
million, and find that the revenue increase is $462 per household that is induced to stop
defecating in the open. In panels B and C of Fig. 3, the range of values generated by
trying different discount rates and using the upper and lower bounds from Table 4 are
displayed; the gains per household are around $200 at the low end and over $1100 at the
top end. These revenue gains associated with improvements in the early-life public health
environment are substantial, and on top of the numerous conservative assumptions made
earlier, we have ignored other potential sources of fiscal gains, such as reduced public
health care expenditures and calorie requirements if sanitation investments lead to
improvements in health among the affected population. Additionally, in Online Appendix F
we present the results of quantile regressions, which show that the association between
the early-life health environment and wages tends to be larger towards the upper end of
the income distribution; as a result, in Online Appendix G.1, we show that the estimated
fiscal benefits using the quantile regression results are even larger than those presented
here. These revenue gains associated with improvements in the early-life public health
environment are substantial, and on top of the numerous conservative assumptions made
earlier, we have ignored other potential sources of fiscal gains, such as reduced public
health care expenditures and calorie requirements if sanitation investments lead to
improvements in health among the affected population. Additionally, in Online Appendix F
we present the results of quantile regressions, which show that the association between
the early-life health environment and wages tends to be larger towards the upper end of
the income distribution; as a result, in Online Appendix G.1, we show that the estimated
fiscal benefits using the quantile regression results are even larger than those presented
here.

<hs>  Consequences for household economic well-being</hs>
  ~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~~

Increases in wages associated with improved early-life health not only raise tax revenues;
they should also lead to higher after-tax income and consumption. In this subsection, we
attempt to quantify these gains in household economic well-being, where, as stated at the
beginning of this section, we loosely interpret increases in household consumption as
gains in welfare. As throughout the article, we abstract from all benefits of better
health and more physically and mentally capable citizens, as we are unable to measure
them, and focus only on the gains from higher consumption. We consider the increase in
consumption associated with the same changes as in the fiscal calculations: a 1% reduction
in IMR today and for the next 100 years, and the elimination of open defecation. Per-
capita GDP was estimated to be $1219 in 2010–11, and given that the 2011 Indian Census
finds that about 40% of the overall population are workers,26 this implies an average
income of $3063 for employed individuals. Tax revenue was estimated to be 10.39% of GDP in
2011, according to the World Bank, so we use a net-of-tax rate of 0.8961, implying after-
tax income of $2745 for the average employed individual, and we continue to use 3.81% as
the annual discount rate, although now this should be understood as either a personal or
social rate of time preference. In our baseline estimates, each 1% point reduction in IMR
is associated with an increase in wages of 1.74%, implying a $47.76 per year increase in
household consumption per average worker. The details of the calculations can be found in
Online Appendix E.2, and the present-value increase in welfare is equivalent to $165.15
billion of consumption; to put this number in context, it is equivalent in welfare terms
to a $6.06 billion (about 0.3% of GDP) increase in annual consumption now and for every
year in the future. Panel A of Fig. 4 displays the robustness of this result to varying
estimates and discount rates, confirming a significant welfare gain that ranges from about
$86 billion to as much as $669 billion. In our baseline estimates, each 1% point reduction
in IMR is associated with an increase in wages of 1.74%, implying a $47.76 per year
increase in household consumption per average worker. The details of the calculations can
be found in Online Appendix E.2, and the present-value increase in welfare is equivalent
to $165.15 billion of consumption; to put this number in context, it is equivalent in
welfare terms to a $6.06 billion (about 0.3% of GDP) increase in annual consumption now
and for every year in the future. Panel A of Fig. 4 displays the robustness of this result
to varying estimates and discount rates, confirming a significant welfare gain that ranges
from about $86 billion to as much as $669 billion. As an alternative robustness check, we
can also use our estimates of the association between IMR and consumption directly.
Average per capita consumption was 1430 and 2630 INR per month in rural and urban areas in
the 2011 NSS; since 68.84% of India is rural, this implies average consumption of 1803.92
INR per month, or $458.41 per person per year. Each 1% point decrease in infant mortality
is associated with an increase in average consumption by 1.73% for everyone in a household
with an affected main earner, or $7.93 per person per year. Adding up these gains as
described in Online Appendix E.2, we find a total welfare gain of $68.91 billion in
present value terms associated with 10 fewer infant deaths per 1000 births. This value is
smaller than the one calculated from the wage regressions, which should not be surprising
as the estimates of per capita consumption in the NSS are considerably smaller than the
after-tax value of per-capita GDP; however, a gain of this magnitude is still economically
very significant. As an alternative robustness check, we can also use our estimates of the
association between IMR and consumption directly. Average per capita consumption was 1430
and 2630 INR per month in rural and urban areas in the 2011 NSS; since 68.84% of India is
rural, this implies average consumption of 1803.92 INR per month, or $458.41 per person
per year. Each 1% point decrease in infant mortality is associated with an increase in
average consumption by 1.73% for everyone in a household with an affected main earner, or
$7.93 per person per year. Adding up these gains as described in Online Appendix E.2, we
find a total welfare gain of $68.91 billion in present value terms associated with 10
fewer infant deaths per 1000 births. This value is smaller than the one calculated from
the wage regressions, which should not be surprising as the estimates of per capita
consumption in the NSS are considerably smaller than the after-tax value of per-capita
GDP; however, a gain of this magnitude is still economically very significant. Meanwhile,
a 1% point reduction in open defecation is associated with a 0.296% increase in wages,
which translates into a $9.07 per year increase in family consumption for an average
worker. This implies that the elimination of open defecation would be associated with
total discounted gains of $4653 for each worker born today; this is equivalent to nearly
four times the current GDP per capita, or about 71.7 years of maximal annual earnings from
NREGA, a large government workfare program. Over the entire workforce, the total present-
value after-tax income gains over the next 100 years or so are $853.99 billion; as before,
this can be expressed as a yearly increase in consumption now and every year in the
future, and in those terms it amounts to $31.3 billion per year, or about a 1.7% increase
in the current GDP of India. Panels B and C of Fig. 4 displays the robustness of these
results; the gains are large at all combinations of parameters, and reach as high as about
$2.1 trillion in total, or $9197 per individual born today. And to emphasize again, all of
these estimates of “utility” impacts refer only to utility from increased consumption, and
not from any other benefits of improved health, cognitive achievement, or mortality; of
course, we also abstract from the complications of calculating welfare in a non-unitary
household. Finally, Online Appendix G.2 evaluates the welfare gains associated with
improvements in IMR and sanitation using the results of the quantile regressions from
Online Appendix F. The quantile regressions suggest that the effect is stronger at high
incomes, and if this is true then the welfare gains should be smaller than in the baseline
analysis if marginal utility diminishes as income increases. Accordingly, using log
utility, we find that the welfare gains are all smaller than those discussed above, but
always highly economically significant, with present-value gains of $33–$74 billion from a
1% point IMR reduction and $412 billion from the elimination of open defecation. Finally,
Online Appendix G.2 evaluates the welfare gains associated with improvements in IMR and
sanitation using the results of the quantile regressions from Online Appendix F. The
quantile regressions suggest that the effect is stronger at high incomes, and if this is
true then the welfare gains should be smaller than in the baseline analysis if marginal
utility diminishes as income increases. Accordingly, using log utility, we find that the
welfare gains are all smaller than those discussed above, but always highly economically
significant, with present-value gains of $33–$74 billion from a 1% point IMR reduction and
$412 billion from the elimination of open defecation. Whichever set of estimates or
procedure for calculating welfare is used, the estimated gains associated with
improvements in early-life health are potentially very large.

<h>CONCLUSION</h>
----------

This article documents a robust gradient between the early-life health environment and
adult wages, decades later. Exploiting heterogeneity across Indian districts in the time-
paths of improvement in infant mortality, we find that men exposed to a better early-life
health environment earned significantly but plausibly higher wages as adults. The
estimated gains are similar across a wide range of specifications and sets of fixed
effects; are replicated in an analysis of historical changes in sanitation; and are
consistent with finding improvements in consumption of similar magnitude, precisely when
the man for whom we have data is the household's main earner. These results are not
spurious consequences of selective migration, which we can observe in our data. Our
results are not driven by changes in education; this is consistent with Bleakley's
Envelope Theorem prediction and with evidence from Cutler et al. (2010) on the effects of
early-life malaria exposure on subsequent consumption in India. Moreover, the apparent
unimportance of education to the health-wages relationship may make certain omitted
variable threats less likely, such as coincidental other improvements in education or
other human capital facilities in the same districts. These findings suggest that early-
life exposure to infectious disease could have appreciable consequences for economic
outcomes in developing countries, especially in contexts such as India's, where relatively
high early-life mortality rates and exposure to high levels of open defecation both
continue today. Relatively modest effects of early-life health on wages – of the magnitude
of the gradients that we estimate – could add up to important fiscal consequences. Because
improving health raises wages and consumption when children become adults, reductions in
infant disease today causes positive fiscal externalities in the future. Wage gains occur
decades after improvements in the early-life health environment, so the present-day
benefit depends on the interest rate. Our results indicate that public investments to
improve the early-life health and disease environment – potentially including efforts to
reduce exposure to open defecation – could improve well-being at a low net present cost to
the government. Because such public investments are under active public debate in India –
where the Prime Minister has announced an ambitious plan to eliminate open defecation by
2019 – these results are of clear policy importance. Nevertheless, we must acknowledge
some important limitations of our analysis. First, because we do not observe the mechanism
assigning different Indian districts to improvements in infant mortality and sanitation at
different times, and because data limitations force us to use long-term trends in these
improvements, we cannot fully confirm the exogeneity of these changes with respect to the
outcomes we study. Second, because we are matching census data with survey data decades
later, and do not longitudinally track individual children as they become adult workers,
we cannot observe mechanisms in a lifetime of health and human capital measurements.
However, Spears and Lamba (2016) have recently documented an effect of early-life exposure
to open defecation in India on later-childhood cognitive achievement, while Spears (2012b)
demonstrates that Indian children who are taller (due in part to better early-life health
and net nutrition) also perform better on learning tests. These prior findings suggest
that our results are plausible, and that cognitive development is one important mechanism
in translating better early-life health into future achievement. Finally, our welfare
analysis of quantitative policy implications must assume a unitary household model,
because our data source does not allow us to observe the consumption of individual members
of the household. Despite these limitations, our results suggest an important role for
early-life health in adult economic outcomes in India.


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