Attribution error in economic voting: evidence from trade shocks.
Hayes, Rosa C. ; Imai, Masami ; Shelton, Cameron A. 等
I. INTRODUCTION
The vast literature on economic voting finds that voters in many
countries reward incumbents for presiding over strong economic growth,
low unemployment, and low inflation and punish for the reverse (Duch and
Stevenson 2008; Fair 1978; Frey and Schneider 1978; Hellwig 2001; Kramer
1971; Lewis-Beck 1988: Powell and Whitten 1993). (1) Other economic
variables such as tax increases have received inconsistent support
(Niemi, Stanley, and Vogel 1995; Kone and Winters 1993) leading reviews
to conclude that there are two main variables of interest: inflation and
gross domestic product (GDP) growth or unemployment (Lewis-Beck and
Paldam 2000; Nannestad and Paldam 1994). (2)
While it is clear that many voters remain ignorant even of these
summary variables (Paldam and Nannestad 2000), voter ignorance is
neither absolute nor randomly distributed. Studies have found age,
education, and income to be significantly related to voters'
knowledge (Blendon et al. 1997: Paldam and Nannestad 2000). (3) Some
voters clearly have the incentive to acquire information, either because
it has personal value in investment decisions or because they feel a
social duty to be informed. Aidt (2000) optimistically cites the fact
that unemployment and inflation can explain about one-third of the
variation of votes in an average election (Nannestad and Paldam 1994) as
evidence that the informed voters are sufficiently influential to
provide at least some discipline for the broader electorate. However,
this line of argument assumes that voters reward outcomes that are
correlated with representatives' skill and effort. Informed voters
may take the time and effort to learn the state of the economy
(macroeconomic aggregates), but may be incapable of distinguishing
between that which can be attributed to the government and that which is
out of the government's control. The motives that lead a voter to
acquire accurate facts rarely require accurate interpretation of the
government's role in generating those facts. (4)
Some authors have argued that voters determine the threshold of
what constitutes acceptable performance by "benchmarking" to
neighboring polities (Besley and Case 1995; Kayser and Peress 2012;
Leigh 2009; Leigh and McLeish 2009). Kayser and Peress (2012) decompose
a country's growth rate into two components: that which is common
amongst neighbors and that which is idiosyncratic to the country in
question. They then show that voters respond only to the idiosyncratic
component, increasing (reducing) support for the incumbent when domestic
growth is higher (lower) than growth among neighbors. Leigh performs the
same decomposition.
But benchmarking does not prevent attribution errors: they are
separate phenomena that can occur independently. Suppose reduced growth
in the United States reduces growth in Brazil owing to trade spillovers
but has little effect on growth in Uruguay, which is less dependent on
U.S. trade. Benchmarking voters would reward Uruguayan politicians for
avoiding the growth slowdown that has afflicted Brazil but they would be
making an attribution error when doing so because the Brazilian growth
slowdown was not due to Brazilian policy and the lack of it was not due
to better decisions by Uruguyan policymakers.
To date, two studies document the presence of attribution errors in
the United States and India. Wolfers (2006) shows that the incumbent
governors of oil-producing U.S. states tend to enjoy a higher reelection
probability when oil prices are rising. Leigh and McLeish (2009) show
that Australian voters reward state governors for both competence
(unemployment in their state relative to the rest of Australia) and luck
(unemployment common to all states). Cole, Healy, and Werker (2012) show
that weather events (e.g., drought) have important effects on voting
outcomes in India even though vigorous disaster relief spending can
mitigate these effects. Hence, voters seem to be erroneously rewarding
their political representatives for shocks that are both similarly
observable and clearly exogenous.
Adding to this literature, we examine the panel data on government
turnovers of 72 democratic countries from 1990 to 2009 and estimate the
extent to which voters erroneously reward or punish their
representatives for economic growth that is driven purely by a change in
the economic conditions of their major trading partners. By extracting
this exogenous component of economic growth that is outside the
incumbent governments' control and estimating its impact on the
probability of government turnover, we attempt to measure the prevalence
of attribution error in a large panel of democratic countries.
Our approach yields several distinctive benefits. First, GDP is
arguably more central to voters' decisions than crisis response.
Second, the aforementioned studies on attribution error focus on one
country (India or the United States) while this article investigates
whether a similar attribution error can be detected in a broad panel of
countries, thereby checking the generalizability of within-country
studies. This is especially important as economic voting is notoriously
context-specific (Lewis-Beck and Paldam 2000). Third, extending to panel
data for a large set of countries allows us to probe whether there are
institutional features that make voter attribution error more or less
severe. For instance, electoral budget cycles constitute an inefficiency
that similarly springs from the agency relationship between voters and
political representatives. It has been shown that countries with greater
media freedom (Akhmedov and Zhuravskaya 2004), greater budget
transparency (Alt and Lassen 2006), more stable parties and thus more
informative party labels (Shelton 2013), and more experience as a
democracy (Brender and Drazen 2005, 2008) are able to suppress these
cycles. The prevailing interpretation is that improving the information
that reaches voters and/or their ability to effectively process that
information enables voters to recognize and punish the inefficient
behavior at the heart of the budget cycle. We test whether these
institutional advantages similarly enable voters to distinguish between
domestic and imported growth.
We find that voters are, on average, sensitive to prevailing
economic conditions: incumbents are more likely to be ousted during a
recession and more likely to remain in office during a boom. While
magnitudes cannot be directly compared, the results are roughly in line
with the existing literature on economic voting. However, we also find
that, on average, voters do not distinguish between growth that is
imported from trade partners and growth that is home-grown. That is,
incumbent governments seem to be rewarded or punished for economic
outcomes that arise from pure luck. The extent of such attribution error
is quantitatively important as well: the estimates suggest that, when
exogenous negative trade shocks push down domestic economic growth by 1
percentage point, the likelihood of an incumbent chief executive (either
the prime minister or the president) being replaced, on average,
increases by 8.2 percentage points, which is substantial, given the
sample average likelihood of chief executive replacement is 58%.
However, the split sample results show that media freedom, experience as
a democracy, and a more educated populace each significantly reduces the
electorate's response to imported (exogenous) growth, suggesting
that institutional context is highly relevant. As a result, the
phenomenon is largely absent from a privileged subsample of countries.
There is relatively little prior work investigating the role of
institutional variables in economic voting and it is limited to studies
of benchmarking rather than those that, such as the current study,
directly measure attribution error. Kayser and Peress (2012) examine
whether economic news is benchmarked but have only a short time series
for a single country. In a full panel, Leigh (2009) observes that higher
GDP per capita and a more educated populace, and perhaps greater media
penetration help reduce attribution error. These measures are not
identical but are similar in spirit to the institutional measures that
have been shown to be significant predictors of voting agency and on
which we focus. Thus, we consider this as evidence that benchmarking and
attribution errors respond to similar sets of characteristics of the
voting population and environment.
The rest of this article is organized as: Sections II and III
describe the methodology and data sources, Section IV reports the
results, followed by concluding remarks in Section V.
II. METHODOLOGY
We follow closely the methodology of Bertrand and Mullainathan
(2001). They compare the impact on chief executive officer (CEO)
compensation of overall change in firm performance with that driven
entirely by "luck" (e.g., industry-wide growth or oil prices)
that should be readily observable to shareholders. (5) Incumbent
electoral success may be viewed as analogous to CEO compensation in that
both jobs are contingent on performance and subject to review by a
supervisory body (in the case of a president or prime minister, this is
the electorate or its representatives). Furthermore, the performance
metrics used to evaluate both CEOs and governments are affected not only
by the quality of their policy decisions, but also by exogenous shocks
outside their control.
Studies of economic voting commonly estimate an equation of the
form:
(1) [T.sub.ie] = [[beta].sub.i] + [[beta].sub.e] + [beta] x
[Y.sub.ie] + [delta][X.sub.ie] + [[epsilon].sub.ie]
where [T.sub.ie] is a dichotomous variable representing turnover
that takes the value 1 if there is a change in government in country i
during year e, [Y.sub.ie] measures GDP growth, [[beta].sub.i] are the
country fixed-effects, which capture country-specific unobservables that
are correlated with the electoral stability of the incumbent government,
[[beta].sub.e] are the election-year fixed effects included to capture
global shocks affecting the probability of government turnover, and
[X.sub.ie] is a vector of country- and government-specific variables
such as the inflation rate or length of time in office which we will
discuss subsequently. The coefficient [beta] captures the average effect
of economic growth on government turnover. It is expected to be negative
if incumbents are less likely to be ousted during economic expansion.
The purpose of this study is to test whether voters make
attribution errors by crediting or blaming incumbent governments for
economic performance that is beyond their control. Conceptually, we may
decompose election-year GDP growth, [Y.sub.ie], into two components:
one, [Y.sup.D.sub.ie] for which the government in country i can
reasonably be held accountable and another, [Y.sup.F.sub.ie], that is
owing to factors outside its control. Rational voters ought to base
their decisions on the first component while filtering out the second.
The aggregate outcome of voter decisions then determines whether the
incumbent government is ousted.
(2) [T.sub.ie] = [[beta].sub.i] + [[beta].sub.e] + [[beta].sub.1]
[Y.sup.D.sub.ie] + [[beta].sub.2] [Y.sup.F.sub.ie] + [delta][X.sub.ie] +
[[epsilon].sub.ie]
The two hypotheses are thus:
H1: [[beta].sub.1] < 0. Accountability. Voters reward (punish)
governments for good (bad) economic performance.
H2: [[beta].sub.2] = 0. No attribution error. Voters do not hold
governments accountable for an observable component of economic
performance that is outside the government's control.
As [Y.sup.D.sub.ie] and [Y.sup.F.sub.ie] are not directly
observable, estimating Equation (2) requires that we find a proxy for
[Y.sup.F.sub.ie] that is orthogonal to [Y.sup.D.sub.ie]. To find such a
proxy, we first project GDP growth onto a weighted average of the growth
of country i's trade partners, which we term imported growth,
[Y.sup.I.sub.ie].
(3) [Y.sub.ie] = [[gamma].sub.i] + [[gamma].sub.e] +
[gamma][Y.sup.I.sub.ie] + [theta][X.sub.ie] + [[mu].sub.ie]
The predicted value from this regression, [[??].sub.ie], is a
component of GDP growth that has been purged of domestic influences and
is thus due to factors outside the government's control. We then
use these predicted values as a proxy for [Y.sup.F.sub.ie] in a
second-stage regression to estimate [[beta].sub.2].
(4) [T.sub.ie] = [[beta].sub.i] + [[beta].sub.e] + [[beta].sub.2]
[[??].sub.ie] + [delta][X.sub.ie] + [[eta].sub.ie]
Note that to estimate [[beta].sub.2] consistently via two-stage
least squares (2SLS), imported growth must satisfy the standard
exclusion restriction for a valid instrument. To test the hypothesis of
accountability, we estimate Equation (1) using ordinary least squares
(OLS) and test [beta] < 0. To test the hypothesis of no-attribution
error, we estimate Equations (3) and (4) using 2SLS (to ensure proper
standard errors) and test [[beta].sub.2] = 0. In each case, standard
errors are clustered by country. (6)
In measuring imported growth, we follow Bruckner and Ciccone (2010)
and Burke (2012) in calculating an "export-weighted
growth-predictor index" (EWGP), based on bilateral trade data. (7)
As argued by Bruckner and Ciccone (2010) and Burke (2012), the effects
of domestic policies are likely to have only second-order effects on
foreign growth rates, thereby making the instrument virtually
independent of changes in domestic political conditions or economic
policies. (8)
To be more specific, we construct the indicator as follows:
(5) [EWGP.sub.it] = [summation over (j [not equal to] i)
[[omega].sub.ij][DELTA][GDP.sub.jt]
(6) [[omega].sub.ij] = 1/T [T.summation over (t=1)]
[Export.sub.ijt]/[GDP.sub.it]
[Export.sub.ijt] is the volume of exports from country i to country
j in year t, which is calculated in current (year t) U.S. dollars.
[GDP.sub.it] is the level of GDP in country i in year t, and is also
calculated in current U.S. dollars. The ratio therefore measures the
contribution to country Vs GDP in year t from its exports to trading
partner j. As in the study by Acemoglu et al. (2008), we average this
ratio over the period 1990-2009 to find time-invariant [[omega].sub.ij],
or a constant average ratio of exports from country i to country j to
country i's GDP in Equation (6). This insulates the instrument from
changes in domestic economic policy (particularly trade policy) and
ensures that the measure depends only on differential effects of trading
partners' economic conditions that are outside the domestic
governments' control. These weights are then used to construct the
export-weighted GDP growth of country i's trading partners for year
t in Equation (5). (9) The instrument has a single-peaked distribution
with mean 0.33 and standard deviation 0.22, and is slightly left-skewed
and fat-tailed relative to the normal. The histogram is included in
Figure A2.
The literature on economic voting typically finds that voters
respond to only a few macroeconomic variables. The "big two,"
as Lewis-Beck and Paldam (2000) put it, are unemployment or GDP growth
and inflation. The literature has also consistently found a "cost
of ruling"; support for the party in power declines even after
controlling for economic performance. Thus, we include inflation and
duration in power as control variables, X, when estimating Equations
(2)-(4). We have also used unemployment data instead of GDP growth but
these data present two major drawbacks. First, lower quality and
coverage result in a smaller, noisier sample. Second, it has been shown
that in some countries, unemployment is a partisan issue with high
levels leading to greater support for left parties even if they are
already in power (Carlsen 2000; Wright 2012). Thus, we focus on GDP
growth and show the results with unemployment data in Table A1 as a
robustness check. Summary statistics of the variables are presented in
Table 1.
Studies of benchmarking, such as Kayser and Peress (2012), use the
difference between a country's growth rate and the average growth
rate of foreign countries to examine whether voters consider the
performance of the domestic economy relative to the average performance
of foreign economies. Unless growth in other countries passes through to
the domestic economy one-for-one, this is not the same as the
domestically generated component of growth that is relevant for proper
attribution. Nonetheless, we do include time fixed effects that capture
global economic conditions and thereby control for benchmarking.
Using country-level data to make inference on individual voting can
potentially run into ecological fallacy. The ecological fallacy is
essentially a problem of unobserved variation hindering the aggregation
from the relationship in individual variables to the relationship
between countrywide averages (Durlauf, Navarro, and Rivers 2010). We
estimate the relationship between a country's voting behavior and a
component of the country's GDP growth rate. It has been shown that
sociotropic voting generally dominates egotropic voting (Lewis-Beck and
Paldam 2000; Nannestad and Paldam 1994). Thus, we are not trying to
infer the relationship between individual votes and individual income
growth (egotropic voting), but trying to infer the relationship between
individual votes and country-wide GDP growth (sociotropic voting).
Arithmetically, if the aggregate vote total responds to aggregate
imported growth, then there must have been many individual voters who
responded to aggregate imported growth.
III. DATA
The main source for political data is the World Bank Database of
Political Institutions (DPI). Following Alesina et al. (1998, 2011), we
construct two binary measures of government turnover to use as the
dependent variables: EXECCH and IDEOCH. EXECCH indicates a change in the
chief executive during an election year. A change in the chief executive
usually results from the electoral loss of the incumbent ruling party in
a parliamentary system or that of the incumbent president in a
presidential system. IDEOCH indicates a change in the ideology of the
cabinet as coded by the World Bank DPI. These measures are strongly
correlated with a correlation coefficient of (.57). (10) Changes in the
executive occur in 177 of the 306 elections (57.8%) whereas changes in
the ideology of the government occur in only 111 of the 306 elections
(36.3%). In practice, a change in ideology is almost always accompanied
by a change in the executive. As a result, IDEOCH is virtually a subset
of EXECCH.
Because the powers of the chief executive, and thus the
public's perception of the chief executive's responsibility,
may vary, we differentiate between countries with parliamentary systems
or assembly-elected presidents and countries with presidential systems.
When calculating the measures of electoral change in leadership, we use
data from executive elections for presidential countries and legislative
elections for parliamentary countries. The preferred specification
combines both systems, but we do check for robustness by limiting to
only parliamentary countries. (11) The main independent variable,
economic growth, represents the percentage change in real GDP. with data
coming from the World Bank collection of World Development Indicators
(WDI). To capture the exogenous component of GDP growth that is driven
by external trade shocks, we make use of bilateral export data available
from the International Monetary Fund Direction of Trade Statistics. To
allow for the broadest possible coverage and avoid an abrupt structural
shift in the patterns of trade, we restrict our analysis to the years
following the end of the Cold War (1990-2009). IV.
IV. RESULTS
A. Baseline Results
Table 2 directly compares the OLS and 2SLS results from estimating
Equations (3) and (4). To demonstrate that the results are fairly
robust, we report the results for several minor variations on the
specification. Columns (1)-(8) include both executive and legislative
elections whereas columns (9)-(16) are restricted to legislative
elections (and thus parliamentary countries). Columns marked
"EXECCH" use the measure of executive change for government
turnover whereas columns labeled "IDEOCH" use the measure of
ideological change for dependent variable. Finally, we vary the length
over which we calculate economic growth. In the specifications marked
"1 Year," economic growth is calculated only for the year of
the election, whereas in the other labeled "2 Years," economic
growth is the average of growth in the election year and the preceding
year. A longer horizon has the advantage of smoothing out measurement
errors but carries the potential disadvantage of overestimating
voters' attention spans that are typically estimated at less than 1
year (Nannestad and Paldam 1994).
The OLS coefficients are all negative, almost all are statistically
significant, and they are all of similar magnitude, indicating that an
additional point of GDP growth reduces the likelihood of replacing the
government by somewhere between 2.2 and 3.8 percentage points. We thus
fail to reject the accountability hypothesis. However, the 2SLS
estimates show a much stronger effect, varying between 4.9 and 11.6
percentage points. To alleviate fears of weak instruments, we follow
Bruckner and Ciccone (2011) in calculating Anderson-Rubin p values that
are robust to weak instruments. The obtained results are significant at
the 5% level for all but one of the specifications (column (14)). The
interquartile range of GDP growth is nearly 4 percentage points,
suggesting that elections conducted in good growth years are roughly
20-45 percentage points more likely to return the government as
elections conducted during bad years. Given the sample average
likelihood of government replacement is either 36% (IDEOCH) or 58%
(EXECCH) depending on the chosen measure of replacement, this is an
extremely large effect. The hypothesis of no attribution error is
clearly rejected.
In the following subsections, we discuss potential sources of
measurement error, add the standard controls, and explore potential
violations of the exclusion restriction. Finally, we add a split-sample
analysis to explore whether certain factors mitigate the attribution
error.
B. Potential Measurement Issues
If voters were correctly ignoring growth that is plausibly
exogenous, we would expect the 2SLS coefficients to be zero. At the
least, we would expect them to be smaller than the OLS coefficients. The
fact that the 2SLS coefficients are larger than the OLS coefficients
likely means that the instrumental variable is mitigating the
attenuation bias in the OLS coefficients that results from measurement
error in the GDP growth data. So long as, after controlling for year and
country fixed effects, measurement error in GDP data are not
contemporaneously correlated between trade partners, estimation by 2SLS
using trade-weighted GDP growth of trading partners serves to purge
domestic GDP of idiosyncratic measurement error as well as the component
of GDP that is due solely to domestic factors. The latter effect should
push the 2SLS coefficient towards zero, presuming voters respond more
strongly to domestic than imported growth. The former should correct the
downward bias in the OLS coefficient. If voters do not strongly
distinguish between imported and domestic growth, the latter could
easily dominate, thereby making the 2SLS coefficient larger than the OLS
coefficient. (12) This may be especially so among less-developed
countries for whom the GDP growth statistics of trade partners are of
much higher quality than those for the domestic economy. (13)
The large discrepancy between the 2SLS and the OLS results suggests
that instrumentation--a step that almost none of the previous literature
in economic voting adopts (Wolfers 2006 being a lone exception)--is of
great importance in estimating the magnitude of economic voting. Prior
insignificant results in this literature may simply be due to
attenuation bias. (14)
Another potential measurement issue derives from the fact that
voters form their opinions using real-time data. As a result, an
econometrician who uses final revision data (as we do) is measuring the
actual variable that went into the voter's decision with error. If
governments systematically manipulate real-time data for electoral gain,
this could introduce bias. (15) There are three cases to consider.
First, the incumbent might inflate growth figures during election years
to increase reelection probabilities. In this case, the effects of
manipulated data will be captured mostly by the intercept as it raises
the reelection probability in all years and countries, regardless of
economic conditions. If certain cultures or institutions enable greater
data manipulation, this will be captured in country fixed effects.
Second, if the measurement error is white noise, then it is the classic
measurement error problem that results in (downward) attenuation bias.
Third, if the extent of data manipulation is systematically related to
the electoral strength of the government, then using the final-revision
data can result in serious omitted variable bias. The two-stage
estimation strategy helps to correct this bias. The first stage strips
the deliberate political misreporting from the domestic GDP growth
numbers (presuming multiple trading partners are not performing the same
political manipulation at the same time). The GDP growth in the second
stage that is predicted based on multiple trading partners' GDP
growth rates is independent of the strength of incumbent governments
that is captured by the error terms. Finally, we have also checked,
using the OECD Economic Outlook, whether GDP data revisions are
systematically different for data released during an election year and
data released in nonelection years. We find no difference using either
quantile-quantile plots or panel regressions.
C. Adding Control Variables
Having established robustness to various methods of constructing
the variables, the remainder of the article uses all elections to
maximize the sample; the IDEOCH indicator rather than EXECCH because
economic policies are more likely associated with a party than a
particular leader; and the 1-year window because the evidence on voter
myopia suggests this is a better fit of voters' time horizons.
Next, we add the two explanatory variables that have consistently been
found significant in the literature on economic voting: inflation and
the length of time the governing party has been in power. The signs are
as expected and significant at the 5% level (Table 3, columns (2) and
(3)): higher inflation and longer time in power both increase the
probability of turnover.
Finally, we add a third control that has recently been suggested by
Alesina, Carloni, and Lecce (2011), and Brender and Drazen (2008):
change in the government budget surplus. Including this variable reduces
the sample, thereby increasing the standard errors enough that the
coefficient loses significance. At the same time, the point estimate
declines slightly. To investigate further, we restrict the sample to
those countries with budget surplus data and use this smaller but
consistent sample to reestimate the specifications from columns (1)-(3)
to produce columns (5)-(7). The point estimates are smaller across these
different specifications, suggesting that adding the change in
government surplus does not reduce the magnitude of the coefficient on
GDP growth, rather the effect is simply weaker in this subsample. (16)
Moreover, as the coefficient on the change in government surplus is
never significant in the regressions, we remove it from further
specifications and revert to the classic specification for economic
voting: the "big two" economic variables plus time in power.
D. Testing the Robustness of the Exclusion Restriction
We report three robustness checks in Tables 4-6. First, one might
be concerned that a home-grown boom or recession reflects off a trade
partner and back to the domestic country. Such an "echo" would
not be exogenous, and it would likely result in an upward bias in the
coefficient on GDP growth in the second-stage regression if voters react
positively (negatively) to the initial home-grown boom (recession). This
is essentially the question of whether the instrument satisfies the
exclusion restriction. If it is indeed violated for certain countries,
then the coefficients ought to decline significantly in magnitude when
we remove the offending countries.
We identify those countries in two different ways. First, we drop
the largest economies: the G7 plus Brazil and India. The echo is
probably larger for the largest economies; for example, recession in the
United States is likely to affect the entire global economy, which is
likely to have sizable effects on the U.S. economy, whereas a similar
recession in Mexico is unlikely to have such feedback effects. Comparing
Tables 3 and 4, we can observe that dropping the largest economies makes
little difference (the magnitude actually increases slightly).
Second, we explicitly calculate the feedback effects for each
country based on the first-stage regression results; that is, we take a
1% impulse to country i's GDP growth and feed it through the
first-stage coefficient and export shares to calculate the predicted GDP
growth in country i's trading partners, then feed the predicted
growth of country i's trading partners through the first-stage
coefficient and export shares to country i to calculate the total
feedback effect. The distribution of feedback effects is displayed in
Figure A1. Note that in most cases, the feedback is less than
one-hundredth of the initial growth in the home country. We exclude the
nine countries with feedback effects >.05 and reestimate the same
regression equations (Table 5). (17) The point estimates decline
slightly in magnitude: between 8% and 12%. Meanwhile, the smaller sample
increases the conventional standard errors: between 2% and 16%.
Nonetheless, the Anderson-Rubin weak-instrument robust tests continue to
reject the null hypothesis of no effect at the 5% level.
Finally, in many countries, the ruling party may call for new
elections when electoral conditions are particularly favorable. (18) As
we cannot observe all of the conditions that favor the ruling party and
thus cannot control for them, we might have sample selectivity problems
as elections called early and those allowed to occur at the mandated
expiration of the term may constitute different samples. To address this
issue, we have rerun the analysis having removed those elections that
were actually held more than a month in advance of the constitutionally
specified time. The results do in fact differ across these samples (cf.
Tables 3 and 6): economic voting is stronger in elections held at the
constitutionally mandated date, so the results are not being driven by
early elections. We believe that the difference arises because snap
elections are frequently called in response to idiosyncratic political
events that are largely orthogonal to the macroeconomic situation. (19)
As a result, snap elections are more likely to be coincident with and
focused on noneconomic issues than regularly scheduled elections.
E. Mitigating Factors
Next, we address whether a free press, an educated citizenry, and a
mature democracy mitigate the extent of this misattribution by voters.
When voters choose whether or not to be informed, they are balancing the
cost of acquiring information against its potential benefit.
Importantly, the cost of acquisition includes both the direct cost
(e.g., subscription price of a newspaper) and the consumption cost of
reading, parsing, and filtering the raw and potentially biased
information to achieve an informative signal. We would expect these
costs to vary across voters. Better-educated voters are likely to have
lower consumption costs and thus be better informed (Aidt 2000). On
aggregate, we expect countries with a more educated population to
respond less to the imported (irrelevant) component of growth as their
more educated voters are more likely to realize that the government is
not responsible for that component of growth.
Similarly, we expect that a free press will provide voters with
higher quality information and thus an easier signal-extraction problem.
Finally, we expect that the process of evaluating a government requires
practice and the evolution of soft institutions dedicated to monitoring;
that the media and the electorate both learn better what information is
relevant and what is not and that as they do so the quality of
information increases and the cost of consumption declines, both leading
to an electorate that is less likely to make attribution errors.
We test these hypotheses by splitting the sample at the median
value for continuous variables (years of schooling and freedom of the
press index) or between the categories for the dichotomous variable (new
vs. established democracies). (20) We run only our preferred
specification: 2SLS using the IDEOCH measure of government turnover, the
shorter l-year window for economic growth, and pooling all elections. We
measure freedom of the press using the Freedom House's Index. We
measure the education level of citizens using the Barro-Lee Educational
Attainment Dataset for average years of schooling in the adult
population. (21) We adopt Brender and Drazen's (2005) definition of
an established democracy as a country that has been through at least
four consecutive democratic elections. We outline the results in Table
7, and report the same sample splits with controls for inflation and
duration in power in Table 8. In both tables, we continue to use the
Anderson-Rubin statistic to test the null hypothesis of no effect in a
manner that is robust to a potentially weak instrument.
The results support the hypotheses that factors improving the
transmission of information can reduce attribution error. In both
tables, voters in new democracies respond strongly to imported growth
whereas those in established democracies do not appear to make such
attribution errors. Likewise, the attribution error is characteristic of
electorates with lower levels of education (the Anderson-Rubin test
strongly rejects the null hypothesis of no effect in both
specifications), but not those with higher levels of education. The
evidence on media freedom is somewhat weaker but points in the expected
direction. It is also worth noting that these three measures are not
strongly correlated and thus appear to measure distinct methods of
improving voters' performance. (22)
V. SUMMARY
How do voters treat their incumbent government in elections when
their economies are in recession or boom? Does it matter to voters
whether the state of the economy is homegrown or imported from trading
partners? We present together a panel data set of 72 democracies from
1990 to 2009 and show that voters do reward incumbent government for
good economic performance. However, they do so even when the economic
boom results from their trading partners' economic boom. These
results suggest that voters make systematic attribution errors by
rewarding incumbents for growth that is plausibly exogenous. However, we
have shown that the same factors which mitigate the electoral budget
cycle also mitigate this form of voter misattribution, suggesting that
voter attribution errors are less likely in countries with a long
tradition of democracy, educated voters, and free media. These results
are robust to exclusion of high-feedback economies, endogenous
elections, and system of democratic government; the inclusion of
standard controls; and choices of how to construct the instrument.
The results highlight an additional potential obstacle to
democratic accountability. Voters may reduce the informational
complexity by focusing on easily understood metrics such as economic
growth and inflation. Voters may pay the costs to acquire such
information out of civic duty or in service of social or personal
financial gains. But even so, voters may not be capable of processing
this information to correctly assign credit or blame to the incumbent
government. The results suggest that reducing such errors requires
educated and experienced voters and a media able to set the information
in its proper context, and thus confirm the growing literature that
touts the importance of the soft institutions of democracy. Improving
the quality of information available to voters and improving, by
practice and education, the ability of voters to process this
information enables voters to better attribute economic performance to
its proper source.
There are three natural extensions of this article. First, the
literature on economic voting explores whether inflation affects
election returns (Lewis-Beck and Paldam 2000; Nannestad and Paldam 1994)
and also the turnover of central bank governors (Dreher, Sturm, and de
Haan 2008). It would be of interest to explore whether imported
inflation has similar effects based on the data on international
monetary linkages as well as trade linkages. Second, the results show
that experience, education, and access to information help reduce
attribution error. Examination of attribution errors with voter-level
microdata is a promising avenue that may further illuminate the
mechanism by which attributor errors occur. Third, although the results
that imported growth has important effects on government turnovers
suggest that voters might not be attributing the source of economic
fluctuation properly, an alternative interpretation is that voters
punish governments for not responding to negative trade shocks
aggressively enough to reduce their effects on the domestic economy.
These are not necessarily competing explanations; they are likely to be
taking place at the same time, potentially reinforcing each other (i.e.,
if voters are not attributing properly, then they might be more likely
to demand explicit policy action to reduce the severity of a recession).
Examination of whether government turnover varies with policy response
is thus another potential avenue of future research.
ABBREVIATIONS
2SLS: Two-Stage Least Squares
CEO: Chief Executive Officer
DPI: Database of Political Institutions
EWGP: Export-Weighted Growth-Predictor
GDP: Gross Domestic Product
OLS: Ordinary Least Squares
PWT: Penn World Table
WDI: World Development Indicators
doi: 10.1111/ecin.12116
Online Early publication July 2, 2014
APPENDIX
[FIGURE A1 OMITTED]
Figure A1 displays the histogram of the estimated feedback effect
of a 1% increase in domestic GDP growth. A 1% shock to GDP in the
domestic country will produce greater GDP in trade partners, which will
then redound to further increases in domestic GDP While most countries
are too small or too closed to generate significant feedback from
domestic shocks, nine countries in the sample exhibit feedback in excess
of 5% of the original shock. The calculation is based upon the
first-stage regression coefficient and export-to-GDP shares of each
country.
[FIGURE A2 OMITTED]
TABLE A1
The Electoral Response to Imported Growth
(unemployment)
Dependent Variable:
IDEOCH (1) (2) (3)
All Elections
Unemployment 0.0668 0.0694 0.0806
(imported) (.376) (.389) (.390)
Length party has been
in power 0.0261 *** 0.0265 ***
-0.00575 -0.00594
Inflation 0.00655
-0.00963
Observations 204 204 204
Number of countries 53 53 53
Kleibergen-Paap
Wald F statistics 2.52 2.48 2.15
Stock-Yogo 15% 8.96 8.96 8.96
critical value
Notes: Table A1 repeats columns (1)-(3) from Table 3
using unemployment instead of GDP growth. The signs are
as expected but the instrument is too weak to allow inference,
p values in parentheses. We use Anderson-Rubin standard
errors, which are robust to weak instruments,
*** p < .01, ** p <.05, * p < .1.
TABLE A2
The Sample Under Different Conditions
Years in Sample
All Legislative All Observations
Elections Elections Elections Lost Due to
with Due to
No No Government Government
Country Controls Controls Surplus Surplus
Albania 6 6 3 3
Argentina 4 -- 3 1
Australia 7 7 6 1
Austria 7 7 6 1
Bahamas 4 4 2 2
Barbados 3 3 3
Belgium 5 5 5
Belize 3 3 1 2
Bolivia 5 -- 4 1
Brazil 4 -- 3 1
Canada 6 6 6
Cape Verde
Islands 4 1 1 3
Chile 4 -- 4
Colombia 3 -- 2 1
Costa Rica 5 -- 4 1
Croatia 4 2 4
Cyprus 3 -- 2 1
Czech Republic 3 3 3
Denmark 6 6 5 1
Dominican
Republic 6 -- 5 1
Ecuador 3 -- 2 1
El Salvador 4 -- 4
Estonia 3 3 3
Finland 5 5 5
France 4 4 4
Germany 6 6 5 1
Ghana 2 -- 2
Greece 6 6 5 1
Grenada 5 5 5
Guatemala 4 -- 2 2
Honduras 5 -- 5
Hungary 5 5 4 1
Iceland 5 5 5
India 5 5 5
Ireland 4 4 4
Israel 7 5 7
Italy 6 6 5 1
Jamaica 4 4 2 2
Japan 6 6 1 5
Latvia 4 4 3 1
Luxembourg 4 4 3 1
Macedonia 3 3 2 1
Malawi 3 -- 3
Malta 5 5 5
Mexico 2 -- 2
Moldova 4 3 3 1
Nepal 3 3 3
The Netherlands 6 6 6
New Zealand 7 7 5 2
Nigeria 2 -- 2
Norway 5 5 5
Pakistan 2 2 1 1
Paraguay 4 -- 4
Peru 2 -- 2
Poland 2 -- 2
Portugal 6 6 6
Romania 2 2 1 1
Senegal 2 -- 2
Slovenia 5 5 4 1
South Korea 4 -- 4
Spain 5 5 5
Sri Lanka 2 -- 2
St. Lucia 4 4 4
Sweden 5 5 4 1
Thailand 2 2 2
Trinidad-Tobago 6 6 3 3
Turkey 3 3 3
Ukraine 2 -- 2
UK 4 4 4
USA 5 -- 5
Uruguay 4 -- 4
Vanuatu 6 6 6
Years in Sample
Years of Media
Democratic Age Schooling Freedom
Country New Established High Low High Low
Albania 3 3 4 1 5
Argentina 2 2 1 3 4
Australia 7 7 6 1
Austria 7 2 4 3 3
Bahamas 4 4 4
Barbados 3 3 3
Belgium 5 5 5
Belize 3 2 1 1
Bolivia 1 4 4 1 3
Brazil 2 2 4 4
Canada 6 5 5
Cape Verde
Islands 4 4 4
Chile 4 1 2 1 2
Colombia 3 3 1 2
Costa Rica 5 5 5
Croatia 3 1 4 4
Cyprus 3 2 2
Czech Republic 3 3 3
Denmark 6 6 6
Dominican
Republic 1 5 5 1 4
Ecuador 1 2 2 1 1
El Salvador 2 2 3 3
Estonia 3 3 3
Finland 5 3 2 5
France 4 2 2 2 2
Germany 6 3 2 5
Ghana 2 1 1
Greece 6 1 4 1 4
Grenada 5 4 2 2
Guatemala 2 2 4 4
Honduras 1 4 4 1 3
Hungary 4 1 3 2 5
Iceland 5 2 3 5
India 5 4 1 3
Ireland 4 4 3 1
Israel 7 6 1 5
Italy 6 1 4 1 4
Jamaica 4 1 3 4
Japan 6 6 3 3
Latvia 3 1 4 4
Luxembourg 4 2 1 3
Macedonia 3 2 1
Malawi 3 2 2
Malta 5 1 3 4
Mexico 2 2 2
Moldova 4 2 1 3
Nepal 3 2 2
The Netherlands 6 6 6
New Zealand 7 6 6
Nigeria 2 2 2
Norway 5 4 4
Pakistan 2 2 2
Paraguay 4 3 3
Peru 2 2 2
Poland 2 2 2
Portugal 6 5 5
Romania 2 2 2
Senegal 2 2 2
Slovenia 5 4 3
South Korea 4 4 1 3
Spain 5 2 2 3 1
Sri Lanka 2 1 1 2
St. Lucia 4 4 4
Sweden 5 5 5
Thailand 2 2 2
Trinidad-Tobago 6 6 1 5
Turkey 3 3 3
Ukraine 2 2 2
UK 4 1 3 3 1
USA 5 4 4
Uruguay 4 3 3
Vanuatu 6 5 1 4
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(1.) See Lewis-Beck and Stegmaier (2013) for a recent comprehensive
review of economic voting literature.
(2.) There is also a large literature that shows the effect of
noneconomic variables such as war casualties (Mueller 1973), fiscal cost
of war (Geys 2010), and natural disasters (Cole, Healy, and Werker 2012:
Healy and Malhotra 2009). We stay clear of these variables because of
difficulties standardizing their selection and measurement across a
large sample of countries.
(3.) There is a related literature, which shows that the quality of
government and its economic policy in just about any measure is strongly
correlated with the level of education (e.g., Barro 1999; Glaeser,
Ponzetto, and Shleifer 2007). Although causation is difficult to
establish (Acemoglu et al. 2005), these results suggest that educated
citizens are better at disciplining their political leaders than
uneducated ones.
(4.) As Caplan (2007) has argued, essentially the entire cost of a
voter's misperceptions falls on the remainder of the electorate,
enabling the voter to indulge in whichever worldview maximizes personal
(often social) benefits. If so, we should note little attempt by voters
to correctly attribute credit and blame, even in situations where
assigning credit is relatively simple.
(5.) Bertrand and Mullainathan (2001) show that CEO compensations
are just as sensitive to a lucky dollar as a general dollar, which they
consider as evidence that managerial agency problems are severe. They
also find that the sensitivity of CEO compensation to a lucky dollar is
closely related to firm-specific measures of corporate governance. The
finding that attribution errors are mitigated in countries where voters
have greater information and experience mirrors their results.
(6.) One might consider an alternative and simpler approach in
which we include imported growth, [Y.sup.I.sub.ie], as well as
[Y.sub.ie], GDP growth, which is observable to voters, to directly test
whether imported growth is discounted in the voters' evaluation of
governments. This equation is hard to interpret, however, because
[Y.sup.I.sub.ie] and [Y.sub.ie] are scaled differently and not directly
comparable as the coefficient on [Y.sup.I.sub.ie] reflects the degree of
pass-through from foreign growth to domestic growth as well as the
extent of attribution error (Bertrand and Mullainathan 2001). Thus, even
if one finds the coefficient on imported growth to be small, it is
difficult to determine whether this is due to small attribution error or
because foreign growth is not very important in determining domestic
growth. The first-stage equation (Equation (3)) circumvents this issue
by properly scaling the effects of imported growth on government
turnover.
(7.) Bruckner and Ciccone (2010) and Burke (2012) use this index,
which fluctuates with the economic performance of close-trading
partners, as an instrument to examine how an externally driven component
of economic growth affects the likelihood of civil conflict risk and
survival of national leader, respectively. Acemoglu et al. (2008)
construct a similar instrument based on trade volume (rather than export
volume) and the level of GDP rather than growth to capture the exogenous
variation in income level that is orthogonal to domestic policy and
institutions.
(8.) We later check the robustness of the results by removing large
economies from the base sample to ensure that our results are not driven
by these large economies whose domestic policies may have feedback
effects.
(9.) We consider several variations of the instrumental variable
constructing [[omega].sub.ij] ratios from different time periods. One
possibility is to use the lagged value of [omega] as a weight. Another
possibility is to construct to based on the pre-1990 data. All measures
are highly correlated with one another (and also with GDP growth) and
generate qualitatively similar results. We choose to construct [omega]
based on the 1990-2009 data as it maximizes the data coverage (bilateral
trade data are spotty) and also to ensure that to does not reflect
important shifts in the domestic environment, some of which might be
anticipated.
(10.) Alesina, Carloni, and Lecce (2011) discuss the advantage and
disadvantage of these two measures. On the one hand, they caution that
EXECCH may falsely identify government turnover if it results from
routine personnel replacement in a stable and reelected government. On
the other hand, if a change in political conditions forces the incumbent
coalition to run under different leadership, then the variable IDEOCH
may underestimate political turnover since were it not for change in
leadership, the incumbent might well have lost the majority.
(11.) We also examine a subsample of countries with a presidential
system, but find that the number of countries in this sample (36
countries) is not large enough to generate informative results.
(12.) See Ashenfelter and Krueger (1994) for detailed discussion of
the property of IV estimates when measurement error and endogeneity
problem are both present.
(13.) For example, Johnson et al. (2009) find that the Penn World
Table (PWT), a widely used GDP growth estimate changes on average by
1.1% across revisions of the dataset. This observation has motivated
many researchers, such as Henderson, Storeygard, and Weil (2012) to seek
creative proxies and instruments to GDP growth rates in developing
countries that limit the effect of measurement error.
(14.) In their review of single-country studies, Duch and Stevenson
(2008, 21) state "in almost no country is there anywhere near the
level of consensus of confidence that characterizes the American
literature." See the rest of this section of their book for a
detailed review.
(15.) Jong-A-Pin, Sturm, and de Haan (2012) show some evidence of
manipulation of budget projections rather than GDP.
(16.) We investigate further with sample splits in the following
section. See Table A2 for the composition of countries in each sample.
(17.) The excluded countries are Belgium, Czech Republic, France,
Germany, The Netherlands, Slovenia, Thailand, UK, and United States.
(18.) We do have some instances of early presidential elections due
to death in office but the lion's share is parliamentary elections
in parliamentary systems.
(19.) For example, the Japanese snap election of 2005 was fought
over the issue of privatizing Japan Post. Incumbent Koizumi won big
despite the weak economy. The New Zealand snap election of 2002 was
precipitated by coalition struggles that were sufficiently arcane that
the election took the opposition by surprise. However, the early
dissolution of both the Israeli and Dutch governments in 2012 stemmed
from failure to agree among the governing coalition to a budget in the
face of economic downturn.
(20.) See Table A2 for the composition of countries in each sample
split.
(21.) See http://www.barrolee.com/ for the Barro-Lee data.
Disclaimer. The views expressed in this article are those of the
authors and are not necessarily reflective of views of the Federal
Reserve Bank of New York or the Federal Reserve System.
ROSA C. HAYES, MASAMI IMAI and CAMERON A. SHELTON *
* We thank anonymous referees, Daniel Riera-Crichton, Tomoharu
Mori, and participants at the Economics Seminar of Wesleyan University,
University of Zurich, Liberal Arts Colleges Development Economics
Conference (Amherst College) for valuable comments. We acknowledge the
financial support from the Quantitative Analysis Center of Wesleyan
University (Hayes and Imai).
Hayes: Senior Research Analyst. Research Group, Federal Reserve
Bank of New York, New York, NY 10045. Phone 1-212-720-8247, Fax
1-212-720-1582, E-mail Rosa.Hayes@ny.frb.org
Imai: Professor, Department of Economics, Wesleyan University,
Middletown, CT 06459-0007. Phone 1-860-6852155. Fax 1-860-685-2301,
E-mail mimai@wesleyan.edu
Shelton: Associate Professor, Robert Day School of Economics and
Finance, Claremont McKenna College, Claremont, CA 91711. Phone
1-909-607-1692, Fax 1-909-6076955, E-mail cshelton@cmc.edu
TABLE 1
Descriptive Statistics
Standard
Whole Sample Observations Mean Deviation Min Max
Inflation
Overall N 299 18.15 131.10 -1.17 2075.89
Between n 71 81.22 0.54 522.93
Within T-bar 4.21 110.70 -501.58 1571.11
Change in central government surplus
Overall N 236 -0.49 2.08 -9.72 5.65
Between n 64 1.06 -2.95 2.02
Within T-bar 3.69 1.82 -8.48 4.10
Duration of party in power
Overall N 301 8.04 8.61 1 71
Between n 72 6.92 2 46.5
Within T-bar 4.18 5.88 -24.46 43.87
Polity score
Overall N 267 8.91 1.54 0 10
Between n 63 1.44 4 10
Within T- bar 4.24 0.76 2.66 11.66
GDP growth
Overall N 306 3.10 3.71 -22.93 12.23
Between n 72 2.55 -11.57 8.37
Within T-bar 4.25 3.11 -8.27 14.46
EWGP
Overall N 306 0.635 0.606 -2.31 2.78
Between n 72 0.420 0.0699 2.15
Within T-bar 4.25 0.452 -1.86 2.19
Two-year growth
Overall N 305 3.24 3.27 -18.58 11.42
Between n 72 2.36 -9.82 8.34
Within T-bar 4.24 2.67 -16.83 12.76
Two-year EWGP
Overall N 306 0.664 0.521 -0.714 0.286
Between n 72 0.402 0.752 0.226
Within T-bar 4.2 0.347 -0.113 0.193
Ideological turnover (IDEOCH)
Overall N 306 0.36 0 1 306
Between n 72 0 1 72
Within T-bar 4.25 -0.44 1.20 4.25
Executive turnover (EXECCH)
Overall N 306 0.58 0 1 306
Between n 72 0 1 72
Within T-bar 4.25 -0.25 1.41 4.25
Unemployment
Overall N 204 8.32 4.91 1.9 35.99
Between n 53 5.23 2.33 34.86
Within T-bar 3.85 2.14 2.47 15.94
TABLE 2
The Electoral Response to Imported Growth
Time Span for GDP
Growth Dependent Variable 1 Year
EXECCH
All Elections [1] [2]
OLS 2SLS
GDP growth -0.0244 *** -0.0494 **
(.00169) (.0173)
Observations 306 306
Number of countries 72 72
[R.sup.2] 0.102
Kleibergen-Paap Wald F 10.25
statistics
Stock-Yogo 15% critical 8.96
value
Time Span for GDP
Growth Dependent Variable 1 Year
IDEOCH
All Elections [3] [4]
OLS 2SLS
GDP growth -0.0219 *** -0.0573 **
(.00919) (.0304)
Observations 306 306
Number of countries 72 72
[R.sup.2] 0.069
Kleibergen-Paap Wald F 10.25
statistics
Stock-Yogo 15% critical 8.96
value
Time Span for GDP
Growth Dependent Variable 2 Years
EXECCH
All Elections [5] [6]
OLS 2SLS
GDP growth -0.0259 *** -0.0629 *
(.00179) (.0551)
Observations 306 306
Number of countries 72 72
[R.sup.2] 0.094
Kleibergen-Paap Wald F 21.01
statistics
Stock-Yogo 15% critical 8.96
value
Time Span for GDP
Growth Dependent Variable 2 Years
IDEOCH
All Elections [7] [8]
OLS 2SLS
GDP growth -0.0278 ** -0.0601 ***
(.00464) (.00262)
Observations 306 306
Number of countries 72 72
[R.sup.2] 0.074
Kleibergen-Paap Wald F 21.01
statistics
Stock-Yogo 15% critical 8.96
value
[9] [10]
Legislative Elections OLS 2SLS
GDP growth -0.0379 *** -0.0704 **
(.000115) (.0499)
Observations 212 212
Number of countries 46 46
[R.sup.2] 0.154
Kleibergen-Paap Wald F 7.94
statistics
Stock-Yogo 15% critical 8.96
value
[11] [12]
Legislative Elections OLS 2SLS
GDP growth -0.0367 *** -0.105 ***
(.00142) (.00114)
Observations 212 212
Number of countries 46 46
[R.sup.2] 0.133
Kleibergen-Paap Wald F 7.94
statistics
Stock-Yogo 15% critical 8.96
value
[13] [14]
Legislative Elections OLS 2SLS
GDP growth -0.0371 *** -0.0863 *
(.000997) (.0541)
Observations 212 212
Number of countries 46 46
[R.sup.2] 0.141
Kleibergen-Paap Wald F 8.59
statistics
Stock-Yogo 15% critical 8.96
value
[15] [16]
Legislative Elections OLS 2SLS
GDP growth -0.0331 *** -0.116 ***
(.00840) (.00378)
Observations 212 212
Number of countries 46 46
[R.sup.2] 0.116
Kleibergen-Paap Wald F 8.59
statistics
Stock-Yogo 15% critical 8.96
value
Notes: This table establishes the basic results for the likelihood
of change in government as a function of GDP growth. The
relationship is estimated first using OLS and then via 2SLS using
the trade-weighted GDP growth rate among trading partners to
isolate the exogenous "imported" component of domestic GDP growth.
We also vary three other specification choices to show the
robustness of the results: GDP growth is calculated either for the
year of the election only (1 year) or as the average of the
election year and the preceding year (2 years); government turnover
is either predicated on the identity of the chief executive
(EXECCH) or on the ideology of the governing coalition (IDEOCH);
and both legislative and executive elections are pooled (all
elections) or the sample is constrained to only legislative
elections (legislative elections), p values in parentheses.
Kleibergen-Paap Wald F statistics show the instrument is borderline
weak. Thus, we use robust standard errors for OLS and
Anderson-Rubin standard errors, which are robust to weak
instruments, for IV.
*** p < .01, ** p < .05, * p < 1.
TABLE 3
The Electoral Response to Imported Growth (with controls)
Dependent
Variable:
IDEOCH (1) (2) (3) (4)
All Elections Base Allowing Sample to Vary
GDP growth
(imported) -0.0573 ** -0.0833 ** -0.0816 ** -0.0607
(.00304) (.00833) (.0268) (.233)
Length party has
been in power 0.0177 *** 0.0219 *** 0.0291 ***
(.000571) (4.22e-05) (5.66e-06)
Inflation -0.00503 ** -0.000194
(.0478) (.968)
Change in
government
surplus 0.0454
(.0394)
Observations 306 301 294 229
Number of
countries 72 71 69 58
Kleibergen-Paap
Wald
F statistics 10.25 11.03 6.946 20.55
Stock-Yogo 15%
critical value 8.96 8.96 8.96 8.96
Dependent
Variable:
IDEOCH (5) (6) (7)
All Elections Consistent Sample
GDP growth
(imported) -0.0496 -0.0494 -0.0494
(.259) (.233) (.235)
Length party has
been in power 0.0289 *** 0.0289 ***
(4.30e-06) (4.32e-06)
Inflation 0.000401
(.935)
Change in
government
surplus
Observations 229 229 229
Number of
countries 58 58 58
Kleibergen-Paap
Wald
F statistics 15.94 15.91 15.64
Stock-Yogo 15%
critical value 8.96 8.96 8.96
Notes: Column (1) is our preferred specification from Table 2: 2SLS
estimator, all elections, IDEOCH indicator, 1-year GDP growth
window. Columns (2) and (3) successively add the two standard
controls in the literature: inflation and the duration the party
has been in power. These strengthen the results on response to
imported GDP growth. Column (4) adds the change in the government
surplus, which has been used in recent studies. Data on government
surplus are sufficiently rare that the standard errors become much
larger and we lose significance when this control is included
(compare columns (1) and (4)). Re-estimating with a consistent
sample, columns (5)-(7), shows that it is the change in sample
rather than correlation among independent variables that is causing
the loss of significance, p values in parentheses. Kleibergen-Paap
Wald F statistics show the instrument is in at least one instance
borderline weak. Thus, we use Anderson-Rubin standard errors, which
are robust to weak instruments.
*** p < 0.1, ** p < 0.5, * p < .1
TABLE 4
The Electoral Response to Imported Growth (no
large economies)
Dependent Variable:
IDEOCH (1) (2) (3)
All Elections
GDP growth -0.0624 *** -0.0912 *** -0.0868 **
(imported) (.00158) (.00690) (.0258)
Length party has been 0.0177 *** 0.0234 ***
in power (.000556) (7.88e-07)
Inflation -0.00537 *
(.0559)
Observations 260 256 249
Number of countries 63 62 60
Kleibergen-Paap
Wald F statistics 9.29 9.44 5.98
Stock-Yogo 15%
critical value 8.96 8.96 8.96
Notes: This table repeats columns (1)-(3) from Table 3
while removing the largest economies (G7 plus India and
Brazil) from the sample to avoid feedback from a domestic
shock reflected through trade links back to the domestic economy.
The results are virtually identical to those of Table 3. If
anything, the response to imported growth is a little stronger, p
values in parentheses. Kleibergen-Paap Wald F statistics show
the instrument is borderline weak. Thus, we use Anderson-Rubin
standard errors, which are robust to weak instruments.
*** p < .01, ** p < .05, * p < .1.
TABLE 5
The Electoral Response to Imported Growth (no
high feedback economies)
Dependent Variable:
IDEOCH (1) (2) (3)
All Elections
GDP growth -0.0500 ** -0.0730 ** -0.0753 **
(imported) (.0187) (.0354) (.0307)
Length party has been 0.0161 *** 0.0196 ***
in power (.00187) (.000305)
Inflation -0.00410 *
(.0983)
Observations 266 260 254
Number of countries 63 62 60
Kleibergen-Paap 8.77 8.46 8.21
Wald F statistics
Stock-Yogo 15% 8.96 8.96 8.96
critical value
Notes: This table repeats Table 3 while removing the
economies with the largest estimated feedback from a domestic
shock reflected through trade partners. We take a 1%
exogenous shock to domestic GDP, use the first stage estimates
of the strength of trade links to calculate the resulting
effect on foreign GDP, and then repeat once more to
calculate the reflected effect on domestic GDP. Countries
with a coefficient of greater than 0.05 are removed from the
sample. This list includes countries with large and/or trade-dependent
economies: Belgium, Czech Republic, The Netherlands,
France, Germany, Slovenia, Thailand, UK, and United
States. Removing weakens the point estimates slightly compared
with those of Table 3 but the Anderson-Rubin statistics
indicate significance at the 5% level, p values in parentheses.
Kleibergen-Paap Wald F statistics show the instrument is borderline
weak. Thus, we use Anderson-Rubin standard errors,
which are robust to weak instruments.
*** p < .01, ** p < .05, * p < .1.
TABLE 6
The Electoral Response to Imported Growth (no
early elections)
Dependent Variable:
IDEOCH [1] [2] [3]
All Elections
GDP growth -0.0949 *** -0.103 *** -0.103 **
(imported) (.00207) (.00167) (.0150)
Length party has been 0.0250 *** 0.0256 ***
in power (4.61e-06) (3.13e-06)
Inflation -0.00669
(.103)
Observations 222 219 211
Number of countries 58 58 56
Kleibergen-Paap
Wald F statistics 7.69 7.76 4.28
Stock-Yogo 15%
critical value 8.96 8.96 8.96
Notes: This table repeats Table 3 while removing elections
that were called early. Early elections are defined to include
those at least 1 month before the constitutionally required
date excepting only the following. Early elections do not
include those that are earlier than expected as the result
of constitutional revisions. While this removes 25-30% of
the data, the magnitude of the coefficient becomes larger
(compare with Table 3). We suspect that elections called early
are often due to political events which call voter attention
from economic issues, p values in parentheses. Kleibergen-Paap
Wald F statistics show the instrument is somewhat weak.
Thus, we use Anderson-Rubin standard errors, which are
robust to weak instruments.
*** p < .01, ** p < .05, *p < .1.
TABLE 7
Mitigating the Response to Imported Electoral Growth
Dependent Variable:
IDEOCH [1] [2] [3]
New Established Low
All Elections Democracies Democracies Schooling
GDP growth (imported) -0.0641 *** 0.00114 -0.242 **
(.000400) (.987) (.0305)
Observations 82 175 158
Number of countries 36 42 56
Kleibergen-Paap Wald F
statistics 2.41 6.07 0.60
Stock-Yogo 15% critical value 8.96 8.96 8.96
Dependent Variable:
IDEOCH [4] [5] [6]
High Controlled Free
All Elections Schooling Media Media
GDP growth (imported) -0.0441 -0.0881 *** -0.156
(.119) (.00137) (.330)
Observations 158 150 131
Number of countries 45 60 44
Kleibergen-Paap Wald F
statistics 13.35 1.86 0.68
Stock-Yogo 15% critical value 8.96 8.96 8.96
Notes: Runs our preferred specification (2SLS estimator, all
elections, IDEOCH indicator. 1-year GDP growth window) while
splitting the sample along four different dimensions. It is shown
that voter response to imported growth is concentrated in new
democracies, countries with low levels of education, and countries
with a high level of trade. The role of a free press is less clear.
p values in parentheses. Kleibergen-Paap Wald F statistics show the
instrument is clearly weak. Thus, we use Anderson-Rubin standard
errors, which are robust to weak instruments.
*** < .01, p < .05, p < .1.
TABLE 8
Mitigating the Response to Imported Electoral Growth (with controls)
Dependent Variable: IDEOCH [1] [2] [3]
New Established Low
All Elections Democracies Democracies Schooling
GDP growth (imported) -0.0779 * -0.0166 -0.238 **
(.0890) (.813) (.0193)
Length of time in power 0.0199 *** 0.0228 0.0308 **
(6.29e-05) (.105) (.0221)
Inflation, consumer prices
(annual %) -0.00279 * 0.00500 0.00119
(.0603) (.431) (.899)
Observations 82 175 158
Number of countries 36 42 56
Kleibergen-Paap Wald F
statistics 1.60 6.27 0.60
Stock-Yogo 15% critical value 8.96 8.96 8.96
Dependent Variable: IDEOCH [4] [5] [6]
High Controlled Free
All Elections Schooling Media Media
GDP growth (imported) -0.0612 -0.348 *** -0.172
(.328) (.000725) (.271)
Length of time in power 0.0171 0.00911 0.0221 **
(.157) (.687) (.0434)
Inflation, consumer prices
(annual %) -0.0127 -0.00301 0.0459
(.571) (.885) (.417)
Observations 158 150 131
Number of countries 45 60 44
Kleibergen-Paap Wald F
statistics 4.06 0.33 0.59
Stock-Yogo 15% critical value 8.96 8.96 8.96
Notes: A repeat of Table 7 with the classic controls: inflation and
duration in power. The results change a little. Voters in countries
with controlled media appear more vulnerable to attribution error,
p values in parentheses. Kleibergen-Paap Wald F statistics show the
instrument is clearly weak. Thus, we use Anderson-Rubin standard
errors, which are robust to weak instruments.
*** p < .0l, ** p < .05, * p < .1.
