Compulsory Voting and Income Inequality: Evidence for ...horiuchi.org/www/Publications_files/lijphart.pdf · Compulsory Voting and Income Inequality: Evidence for Lijphart’s Proposition

Compulsory Voting and Income Inequality:

Evidence for Lijphart’s Proposition from Venezuela

John M. CareyYusaku Horiuchi

ABSTRACT

What difference does it make if the state makes people vote? The question is centralto normative debates about the rights and duties of citizens in a democracy, and tocontemporary policy debates in a number of Latin American countries over whatactions states should take to encourage electoral participation. Focusing on a rarecase of abolishing compulsory voting in Venezuela, this article shows that not forc-ing people to vote yielded a more unequal distribution of income. The evidencesupports Arend Lijphart’s claim, advanced in his 1996 presidential address to theAmerican Political Science Association, that compulsory voting can offset class biasin turnout and, in turn, contribute to the equality of influence.

What difference does it make if more or fewer people vote? What differencewould it make if the state made people vote? These questions are central to

normative debates about the rights and duties of citizens in a democracy (Lacroix2007; Lever 2010) and to contemporary policy debates over what actions statesshould take to encourage electoral participation (Ellis et al. 2006). They are also cen-tral to a surge of research examining the effects of compulsory voting in Latin Amer-ica on important topics, ranging from the rate of invalid ballots cast in elections(Kouba and Lysek 2016) to overall satisfaction with democracy (Singh 2016) andfrom the rise of “outsider” presidential candidates (Carreras 2012) to the condi-tional effect of social assistance programs on electoral support for incumbent parties(Layton and Smith 2015).

To make contributions to these debates and recent studies, this article focuseson the political and policy consequences that followed a rare case of abolishing com-pulsory voting in Venezuela. Specifically, it provides empirical support for theproposition that compulsory voting can reduce income inequality.

In his 1996 presidential address to the American Political Science Association,Arend Lijphart contended that class bias, “the inequality of representation and influ-

Copyright © 2017 University of MiamiDOI: 10.1111/laps.12021

John M. Carey is a professor of government at Dartmouth College. [email protected]. Yusaku Horiuchi is a professor of government and Mitsui Professor of Japan-ese Studies at Dartmouth College. [email protected]

LAPS_Summer2017_LAPS_Fall13_copy.qxp 4/27/2017 11:33 AM Page 122

ence . . . not randomly distributed but systematically biased in favor of more privi-leged citizens . . . and against less advantaged citizens,” is the central “unresolveddilemma” of democracy (Lijphart 1997, 1). The normative foundation of this argu-ment is that in a democracy, the preferences of every citizen should have equalweight in determining policy. Lijphart contends that “low voter turnout meansunequal and socioeconomically biased turnout . . . [and] unequal participation spellsunequal influence” (2). From this, he concludes that compulsory voting is “thestrongest of all the institutional factors” (8) in its potential to remedy the perniciouseffects of class bias in turnout.

Lijphart’s presidential address, published in the American Political ScienceReview, has been cited widely and has motivated many scholars to investigate theimpact of voter turnout on electoral outcomes. Empirical studies, however, havefaced an array of challenges. Simple cross-sectional regressions lack a convincingidentification strategy for causal inference. Instrumental variables based on exoge-nous “shocks” to turnout (e.g., weather events) are irrelevant to Lijphart’s centralclaim that the level of voter turnout, influenced by whether voting is compulsory ormandatory, would affect policy outcomes.1

Two recent studies address these methodological concerns and focus on theintroduction of compulsory voting in Australia (Fowler 2013) and in Austria (Bech-tel et al. 2015). By examining subnational units that adopted compulsory votingwithin federal systems, these studies gain analytical leverage in examining a counter-factual question: what would have happened if compulsory voting had not beenintroduced? Consistent with Lijphart’s proposition that compulsory voting mitigatesclass bias in voter turnout, they connect increases in voter turnout, support for leftistparties (or policy positions), and government spending to compulsory voting. Thesubnational effects they estimate, however, do not map directly onto national-levelpolicy outcomes, which are often subjects of both scholarly and political debate.

This study extends this line of inquiry by examining the abolishment of com-pulsory voting in Venezuela in the early 1990s. Venezuela is one of a few countriesthat enforced compulsory voting for a long period but then dropped it. Amongthese cases, Venezuela offers the most promising environment to study downstream,national-level political and socioeconomic consequences of turnout bias—the ulti-mate outcome variable for Lijphart. The other countries are not suitable for thisinquiry because they abolished compulsory voting before reliable data on economicinequality were available (Spain and the Netherlands), abolished it too recently toestimate downstream effects (Chile), or retained the legal requirement in someregions after the national-level statute was eliminated (Switzerland and Austria).

This article proceeds to review Lijphart’s theory, along with the evidence forits various elements in the empirical literature from Latin America and other con-texts. It goes on to provide an in-depth qualitative study of the Venezuelan case. Itpresents quantitative evidence by running difference-in-differences regressionmodels that estimate the effect on income inequality. The results suggest that notforcing people to vote yielded a more unequal distribution of income in Venezuelathan would have obtained had compulsory voting been maintained. The article

CAREY AND HORIUCHI: COMPULSORY VOTING AND INEQUALITY 123


then discusses alternative interpretations and shows the results of further tests.Noting that Hugo Chávez’s election later in the 1990s fundamentally alteredVenezuela’s electoral landscape, the concluding section discusses what the study’sresults can and cannot say about the Chávez phenomenon, along with broaderpolicy implications.

LIJPHART’S THEORYOF UNEQUAL INFLUENCE

Lijphart’s central argument is that compulsory voting is the strongest remedy forunequal political influence due to unequal turnout. An observable implicationderived from the argument is that income is more unequally distributed whenvoting is voluntary than if it were compulsory. Making the underlying assumptionsin Lijphart’s theory explicit is key to understanding the mechanisms connectingcompulsory voting and income inequality.

The first assumption is that socioeconomic status is a proxy for preferencesabout economic policies that reduce inequality. Specifically, Lijphart assumes thatthe poor prefer policies that minimize inequality more than the rich do. Such poli-cies include progressive taxation on incomes and comprehensive tax deductions forthe poor. Just as important—given that economically less advantaged people aremore susceptible to job market fluctuation and more dependent on public sectorjobs—the poor should have a stronger preference than the rich for public spending(Mainwaring et al. 2015).

The second assumption is that when voting is voluntary, its net utility is greaterfor the rich than for the poor. There are various reasons that this might be the case.For example, the rich might have more riding on policymakers’ decisions. In a coun-try where only a minority earns sufficient formal income to pay income taxes, mar-ginal tax rates will be of little consequence to most citizens but highly salient to therich (Kasara and Suryanarayan 2015). Voting may also be more onerous for thepoor. Poverty corresponds everywhere with low education levels, so the effortsrequired for voters to gain information about candidates and policy platformsshould be larger for the poor than the rich (Downs 1957; Matsusaka 1995).2 Thecosts can also be logistical. The poor may lack transportation or flexible work sched-ules that allow access to the polls.

In short, when voting is voluntary, turnout should be higher among the richthan the poor; that is, there should be a positive socioeconomic bias toparticipation.3 Such bias is strong and longstanding in the United States (Jackson etal. 1998; Leighley and Nagler 1992), and has been documented in various othernational contexts as well (Carlin and Love 2015; Hooghe and Pelleriaux 1998; Jait-man 2013; Irwin 1974; Martikainen et al. 2005; Singh 2011a; Tingsten 1937).4

The third assumption is that imposing sanctions on nonvoters should mitigatethis bias. This should be the case particularly insofar as sanctions such as fines weighmore heavily on the poor than the rich.5 Previous studies have shown that voterturnout is high as long as compulsory voting is enforced with substantial punish-

124 LATIN AMERICAN POLITICS AND SOCIETY 59: 2


ments (Fowler 2013; Jackman 2001) and that socioeconomic bias in turnout is mit-igated under compulsory voting (Singh 2011b, 2015; Carlin and Love 2015).

Conditional on these first three assumptions made by Lijphart, the medianvoter’s position is expected to shift to the right under voluntary voting relative tocompulsory voting. The final assumption is that the elected government respondsto shifts in the median voter’s preference.6 As a result, when compulsory voting isintroduced (or abolished), the elected government should pursue policies that resultin making the distribution of income more (or less) equal.

Following Lijphart’s theory and the logical assumptions underlying it, a shiftfrom compulsory to voluntary voting is expected to draw the following observableimplications: a decline in voter turnout, a shift to the right in the preference of thewealthier median voter, the election of politicians who support less redistribution,the implementation of less progressive economic policies, and an increase in eco-nomic inequality.7 We will examine the empirical validity of the first four effects inthe context of Venezuela, and then examine the validity of the fifth and final effect.

THE CASE OF VENEZUELA

Throughout the late 1970s and 1980s, Venezuelans’ confidence in their political insti-tutions declined. In response, the government adopted a variety of electoral reformsduring the time period under consideration. In 1984, President Jaime Lusinchi cre-ated the Presidential Commission on the Reform of the State (COPRE) to proposereforms aimed at reestablishing citizen engagement and trust. COPRE-initiatedreforms included direct elections of mayors and candidate-preference votes within listsfor municipal councilors in 1988, direct elections of state governors in 1989, and thenin 1993 the introduction of a mixed system for the Chamber of Deputies, togetherwith the end of compulsory voting. These latter two reforms are of particular interestbecause of their potential connection to the politics of redistribution.

From 1958 to 1988, Venezuelan legislators were elected using a closed-list pro-portional representation (PR) system, with the country’s states as districts. The 1993reform shifted Chamber of Deputies elections to a mixed-member system resem-bling Germany’s, in which half the seats are contested by plurality in single-memberdistricts (SMDs) and the other half are allocated to achieve overall proportionality.The electoral law of 1958 also established compulsory voting, along with the specificsanctions for nonparticipation, which included restrictions on employment for, orcontracting with, public entities; on conducting bank transactions; on holdingpublic office; on securing a passport or traveling outside the country; and onenrolling in a state university, all for a period of six months after the election inwhich a citizen did not vote (Rosales 1986). Congress eliminated sanctions in theOrganic Suffrage Law of 1993 (Molina and Pérez Baralt 1995, 1996).8

The coincidence of proportional elections and compulsory voting raises thequestion of whether the former change affected the politics of income inequality.Both Austen-Smith (2000) and Iversen and Soskice (2006) argue that PR electionsencourage, and SMDs discourage, progressive redistribution. Scholarly debate on the



effects of SMD versus PR on redistribution has not yet concluded. Chang et al.(2011), for example, make the converse argument that SMD competition yields poli-cies with diffuse economic benefits and PR encourages concentration of benefits.

In the context of Venezuela’s electoral reform, we believe that there are reasonsto be cautious about applying either model proposed by Austen-Smith (2000) orIversen and Soskice (2006). First, although Venezuela’s reform created SMD com-petition for half the Chamber’s seats, the overall distribution of seats remained pro-portional, mitigating the Duvergerian imperative of SMD competition on whichboth models depend. Second, in the Iversen and Soskice model, the redistributiveeffect is driven by differences between multiparty and two-party parliaments in theformation of coalition governments, whereas Venezuela was, and remains, a presi-dential system. For these reasons, we argue, the theoretical grounds to expect animpact on income distribution from abandoning compulsory voting are strongerthan from the shift to a mixed electoral system. Nevertheless, it is worth taking seri-ously the prospect that the mixed system reform could affect economic inequality,and we return to test the proposition empirically in a later section. For now, wefocus on the logical sequence underpinning Lijphart’s theory of compulsory voting.

The first link in that causal chain is that turnout should decline when compul-sory voting is abandoned. This effect was clear and well documented in theVenezuelan case (Molina 1995; Molina and Pérez Baralt 1995). Voter turnout innational elections had been above 75 percent in every election since the adoption ofcompulsory voting. Specifically, it was 80 percent in 1958, 75 percent in 1963, 92percent in 1968, 90 percent in 1973, 79 percent in 1978, 83 percent in 1983, and80 percent in 1988 (Molina 1995). As soon as sanctions for nonvoting ceased, inthe 1993 election, however, turnout sharply dropped to 54 percent, 20 percentagepoints below the lowest turnout during the period with compulsory voting.

The second link holds that the turnout drop should be concentrated moreheavily among poorer voters than wealthier voters, diminishing demand for progres-sive redistribution. Venezuelan surveys provide some leverage here, although thedata are less than ideal (Baloyra and Torres 1983; Canache 2002). A pre-electionsurvey in 1983 that asked voters to recall their participation ten and five years ear-lier, in the 1973 and 1978 elections, found 6.9 percent and 10.4 percent gaps,respectively, in reported participation between the top and bottom income quartiles.A 1995 survey asking voters to recall participation in the 1993 election produced acorresponding gap of 12.4 percent. This may suggest a widening gap after the abol-ishment of compulsory voting, but the increase is only a marginal one and subjectto all the limitations of respondents’ recall over long time periods.

Surveys that asked more directly about the effects of compulsory voting showmore pronounced differences across income groups. The 1983 survey mentionedabove, for instance, asked whether respondents intended to vote in the upcomingelection that year, and whether they would vote if voting were not compulsory(Baloyra and Torres 1983). Virtually all respondents, regardless of socioeconomicstatus, expressed an intention to vote, but only 25 percent of those in the lowestincome quartile indicated they would do so if voting were not compulsory, com-



pared with 54 percent in the top income quartile. Similarly, a survey conducted in1993, two months before compulsory voting was struck from the electoral law,asked whether respondents would vote that year if voting were not obligatory. Thesurvey dichotomizes all respondents into a low-income group (88 percent of respon-dents) and a high-income group (12 percent), but one-third of the poorer respon-dents said they would not vote if it were not compulsory, as compared with one-fifth of the wealthier group (CIEPA 1993). Subject to the limitations of these data,there is suggestive evidence that compulsory voting diminished socioeconomic biasin participation below levels that would apply under voluntary voting.

Beyond the size and composition of the electorate, the next places to look foreffects are in electoral outcomes—which parties and politicians are elected—and intheir policies that affect the distribution of wealth. The period of our investigationwas one of enormous turbulence, economically and politically, following decadesduring which Venezuela had been regarded as an island of relative prosperity andstability in a much stormier Latin American sea. Venezuelan democracy during thisperiod has been well chronicled (Coppedge 1994, 1996; Crisp 2000; Karl 1997).Does that history suggest a shift in the median voter’s preference?

For our purposes, the top panel of figure 1 provides a schematic of party com-petition from the 1960s through the 1980s, when Venezuelan elections were dom-inated by the center-left social democratic Acción Democrática (AD) and thecenter-right Christian Democratic (COPEI) parties, with a regular, much smallerelectoral presence of smaller parties, under varying labels, on the left. AD andCOPEI dominated all seven national elections from 1958 to 1988, taking morethan 85 percent of the votes between them in each of the last four contests.Throughout the long period in which voting was compulsory, Venezuelans grewfamiliar with a set of options with established locations on a left-right ideologicalspectrum. The center-left AD had the strongest claim to Venezuela’s median voter,winning five of seven presidential elections from 1958 to 1988.

By 1993, however, Venezuela had experienced a period of economic crisis andpolitical discontent under AD president Carlos Andrés Pérez. The contest forCOPEI’s presidential nomination that year split the party. Rafael Caldera, who hadfounded COPEI in the 1950s and had served as president from 1968 to 1973, hadresuscitated his political career with a speech in the Senate in 1992 decrying the dis-proportionate burdens that economic reforms at the time were imposing on thepoor. Caldera’s attempt to recapture COPEI’s nomination for the presidency failed,however, and he bolted the party to run with the backing of a coalition of smallerparties spanning the ideological spectrum (Buxton 2003; Di John 2005). The coali-tion ran under the banner Convergencia.

The second panel of figure 1 locates the main presidential contenders in the1993 election according to the most comprehensive data on ideological placementof presidential candidacies in Latin America (Baker and Greene 2011).9 Specifically,it shows each party’s ideological position on a continuous scale ranging from 1 (left-most) to 20 (rightmost). AD (ideological position = 11.4), discredited by Pérez’spresidency, hemorrhaged voters to its competitors on both flanks. Causa Radical



(ideological position = 7.9) was one beneficiary, more than doubling the left’s tra-ditional vote share, but on the right, Caldera’s Convergencia and the rump COPEI(ideological position for both camps = 14.8) won a majority of the vote. In the four-way race, Caldera’s 31 percent was sufficient to capture the presidency.

This account of events is consistent with Lijphart’s premise that moving fromcompulsory to voluntary voting should produce a class bias in abstention thatpushes the median voter right, diminishing demand for progressive redistribution.To recap, the center-left AD dominated elections during the period with compul-sory voting, but the winner of the first election without compulsory voting in 1993,Caldera, was center-right.

Before embracing this interpretation unconditionally, however, it is importantto acknowledge that narrative accounts of Venezuelan politics in this period portraya fluid electoral environment in which ideological locations of candidacies were hardto pin down. When he was elected in 1988, AD’s Pérez had, like Caldera, previouslyserved as president—in his case, from 1973 to 1978, during an oil boom. Venezue-lans associated Pérez with generous government spending, and he did little to dis-suade this expectation during his 1988 campaign (Buxton 2003). Once inaugu-rated, however, Pérez imposed an economic austerity package described as the GranViraje (Great Turnaround). Cuts in fuel subsidies translated into public transporta-tion rate hikes, which in turn sparked a series of riots in February 1989 known asthe Caracazo. Pérez called out the military, whose heavy-handed response left morethan 350 dead (Di John 2005).

The president’s approval ratings dropped from about 50 percent to 35 percentduring his first year in office (Stokes 2001). His presidency never fully recovered. It


Figure 1. Electoral Politics in Venezuela, 1973–1998

Note: The percentages in parentheses are vote shares.


was threatened by two separate military coup attempts in 1992, neither successful,but the first of them made a media celebrity out of a young colonel with a gift forpopulist rhetoric, Hugo Chávez. A scandal involving government appropriationsprompted Pérez’s removal from office and replacement by an interim president forthe last year of his term. When he ran in 1993, Caldera excoriated the economichardship imposed on the poor under Pérez’s administration (Buxton 2003). Pérez’sGran Viraje had pulled the AD to the right, and Caldera’s 1993 incarnation was aneffort to move left from the traditional COPEI that Caldera himself had helped tofound four decades earlier.

This alternative narrative raises the question of whether the 1993 electoralresult genuinely represented a rightward shift. The longstanding reputations of themain actors, as well as the most authoritative dataset on candidate ideologies, sug-gest that it did (Baker and Greene 2011). Yet the electoral environment was tumul-tuous, and the traditional party system was disintegrating. For a clearer picture ofthe political and economic flux of those years, we turn to the economic policies thesesuccessive administrations pursued.

Figure 2 plots the share of GDP accounted for by government consumption ofgoods and services, plus government (gross) investment expenditures, against (net)Gini coefficients, our measure of inequality after government taxes and transfers.10The vertical bars show the 95 percent confidence interval for the Gini estimates.Government consumption levels (gray dots) bounced around during Carlos AndrésPérez’s second term (1989–93), on net decreasing from just above 32 percent in1989 to just above 30 percent in 1993. The 1993 level, however, is barely below thelevel from 1988, the year before Pérez’s Gran Viraje package of economic reforms.Overall, given the measurement error inherent in the Gini coefficients, there is nostatistically discernible movement in inequality during the Pérez years. This is animportant but perhaps counterintuitive finding. Pérez is often portrayed as the pres-ident who promoted drastic neoliberal reforms, but neither the government share ofGDP nor the Gini coefficient changed substantially during his term.

The pattern becomes dramatic only under Caldera’s administration (black dotsin figure 2), when government spending dropped sharply and monotonically, withcorresponding increases in our measure of inequality. The negative correlation(−0.76, 1989–98) between these variables suggests that the post-1993 austerity poli-cies were an important determinant of the increase in inequality.

Summary

Venezuelan politics from 1988 to 1998 were buffeted by an array of forces broaderthan just the end of compulsory voting, but the available evidence we encounter isconsistent with the proposition that the end of compulsory voting decreased partic-ipation, increased socioeconomic bias, and pushed the center of gravity in theVenezuelan electorate to the right. The policy changes that ensued increasedinequality. Although Pérez’s Gran Viraje is often characterized as a pivotal momentin accounts of Venezuelan politics of the period, neither the share of the economy



accounted for by government spending nor conventional measures of incomeinequality changed under his government. The economic data suggest that it wasCaldera’s administration that exposed, more systematically, the vulnerability of thepoorest Venezuelans.

ESTIMATING THE EFFECTON INEQUALITY

We now examine more systematically the final and most consequential effect ofLijphart’s theory: the effect of abandoning compulsory voting on income inequality.Before introducing our data, statistical models, and findings, we should respond to apotential criticism derived from the fact that ours is inherently a single-country study.

One may argue that it is impossible to make any causal interpretation focusingonly on Venezuela.11 We acknowledge that a simple time series analysis without any


Figure 2. Government Share of GDP and Net Gini Coefficient in Venezuela,1988–1998

Note: The vertical axis shows the averages of multiply imputed Gini coefficients in the SWIIDdata. The vertical lines associated with them indicate the 95 percent confidence intervals. The Gov-ernment Share of GDP includes government consumption of goods and services and government(gross) investment. In each of the six years up through 1993, Government Share of GDP switcheddirection (i.e., rising, falling, rising, etc.), whereas it declined monotonically starting in 1994. Sources: Feenstra et al. 2013; Solt 2009, 2013.


comparison unit does not warrant causal interpretation. Our approach, instead, isto apply a difference-in-differences design.12 Our comparison units are a set of LatinAmerican countries that are similar to Venezuela in important respects. This sectionexplains the selection of comparison units, time periods, and statistical models. Thenext section addresses key questions confronting any analysis of the consequences ofa specific policy change: was the change intentional? and did other changes occurat the same time?

Data

To measure income inequality, we rely on the net (i.e., after-tax, after-transfer) Ginicoefficient as measured by the Standardized World Income Inequality Database(SWIID), Version 4.0 (Solt 2009, 2013). An advantage of using the SWIID datasetis that it has greater coverage across countries and over time than any other cross-national income inequality database. Specifically, by combining a variety of existingdata, including the United Nations University’s World Income Inequality Database(WIID) and the Luxembourg Income Study (LIS), the SWIID dataset providescomparable Gini coefficients for 173 countries for as many years as possible from1960 to 2012.13

The question we examine in this statistical analysis is, what was the estimatedtrajectory of income inequality had Venezuela not experienced a change in 1993?To examine this counterfactual question, we apply a difference-in-differences designusing cross-national, time series data. In this design, it is important to choose a setof countries that share historical, political, economic, and social context withVenezuela. Specifically, we choose the Latin American and Caribbean countries thatwere net oil exporters as of 1993: Argentina, Bolivia, Colombia, Ecuador, Mexico,and Trinidad and Tobago. These countries share similar regional economic condi-tions; moreover, focusing on oil exporters is relevant because the abundance of nat-ural resources is often correlated with both economic growth and disparity.14 It isimportant that none of these countries introduced or abolished compulsory votingduring the period of investigation. Venezuela is the only “treated” case in which therequirement to vote in elections changed.

Specifically, we use three periods of investigation, 1978–98, 1983–98, and1988–98. The numbers of observations are 127, 102, and 76, respectively. Thecoefficient estimates using shorter periods are less efficient, due to smaller numbersof observations, but country-specific trend variables, which we will introduce shortly,may more accurately capture subtle fluctuation in income inequality in each coun-try. Since we do not have a priori a theoretical expectation about the “right” periodof investigation, we try the three different periods.

These periods include four elections: those of 1978, 1983, and 1988—the lastthree elections before the elimination of sanctions in Venezuela—and the subse-quent 1993 election. We do not extend the postreform period beyond 1998. The1998 presidential election was marked by the landslide victory of Chávez, who hadattempted a coup d’état in 1992 and who remained in the presidency until his death



in 2013. The rise of Chavismo is expected to add additional systematic variation tothe post-1993 trajectories of income inequality. This means that the longer thepostreform period for our analysis, the more difficult it would become to interpretthe direct effect of “treatment” (i.e., in our case, the change that occurred in 1993).Methodologically, post-1993 changes in politics and policies are “posttreatment”events, which are partly consequences of the reform in 1993. Incorporating post-treatment factors into our statistical analysis and estimating mediation effects wouldintroduce methodological challenges beyond the scope of this article (Imai et. al.2011; Rosenbaum 1984).

Statistical Models

The difference-in-differences design is a technique with a long tradition in social sci-ence research aimed at estimating the effect of an event, intervention, or “treat-ment.” It uses time series observations that include periods both prior and subse-quent to the event—in our case, the abolishment of compulsory voting in Venezuelain 1993.15 We run the following regression model using the cross-national and timeseries data.

Yit = b0 + b1T1it + b2T2it + fi (t) + vi + ut + eit

The outcome variable Yit is the net Gini coefficient for country i in year t. Thebase category (i = 0, t = 0) is Venezuela in 1993. Accordingly, the intercept coeffi-cient b0 predicts the Gini coefficient in Venezuela in 1993. There are two treatmentvariables. The first treatment T1it is 1 for Venezuela after 1993 (exclusive), while itis 0 otherwise. Formally, T1it = 1(i = 0, t > 0). The second treatment T2it is thenumber of years since 1993 for Venezuela, T2it = t · 1(i = 0, t > 0). While the coef-ficient b1 measures the average change in the outcome variable in Venezuela after1993, the coefficient b2 measures the annual increase in the outcome variable inVenezuela after 1993. After running this model, we then undertake a Chow test(Chow 1960). The null hypothesis we intend to reject is that these coefficients arejointly zero: H0: b1 = b2 = 0; namely, there is no “structural break” in Venezuela in1993.

The model also includes country-specific trend variables fi(t), country-specificfixed effects vi, and year-specific fixed effects ut. The last term eit denotes a stochasticdisturbance. Since we do not have a priori theory on the functional form for thecountry-specific trajectories of the Gini coefficient during the entire period of inves-tigation, we repeat the analysis using linear and quadratic trends. In total, we run sixregression models: three periods (1978–98, 1983–98, and 1988–98) × two func-tional forms (linear and quadratic).16

We do not add other country-specific and time-variant covariates for two rea-sons. First, as we discussed earlier, the postreform observations for these country-specific and time-variant variables are likely to be influenced by the reform of 1993itself. Therefore, adding these variables could introduce posttreatment bias (Rosen-



baum 1984). The observations before the reform are obviously not influenced bythe reform itself, but we assume that the average effects of these variables on the out-come variable are, to a large extent, captured by the country-specific trend variables.Furthermore, the country-specific and year-specific fixed effects control for anycountry-specific attributes (for example, demographics, or political and economichistory) and any time-specific attributes (for example, years in which major eco-nomic shocks occurred at the global level, such as changes in the prices of naturalresources and financial commodities).

In addition, we note an important assumption required for a valid difference-in-differences design, which is called the parallel-trend assumption. Conditional onall country-specific fixed effects, year-specific fixed effects, and country-specifictrend variables, we assume that the trends in the outcome variable during the pre-treatment period are similar among the countries included in our analysis. Moreimportant, conditional on these variables, the outcome variable for the treatedgroup would have been the same, had there been no treatment, as the trend in theoutcome variable for the untreated group. Since this assumption for causal identifi-cation is about the difference in two potential outcomes, it is fundamentally unver-ifiable. In practice, researchers must assume that there was no important change—other than the treatment itself—that influenced the trajectory of the outcomevariable in the treated group. The importance of this assumption motivates ourplacebo tests using the cases of Trinidad and Tobago and Bolivia.

Results

Regression results are presented in table 1. Column P shows that the null hypothesisof no structural break in Venezuela in 1993 can be rejected in four of six models atthe 5 percent level and at the 10 percent level in a fifth, suggesting that the trajectoryof the Gini coefficient systematically changed in Venezuela in 1993.17

Instead of interpreting how the trajectory changed by examining the coefficientestimates for the intercept and the two treatment variables (b^0, b

^1, and b

^2) presented

in table 1, it is more intuitive to compare the factual and counterfactual trendsgraphically. Figure 3 summarizes this analysis for the period from 1983 to 1998.The height of each gray bar is the observed value of the Gini coefficient inVenezuela, whereas the solid dots are predicted values based on our regression analy-sis (see table 1, 1983–98, Linear).18

Venezuela’s Gini coefficients gradually decreased from about 43 percent in1983 to about 38 percent in 1992. This pattern changed after 1993, and the Ginicoefficient increased to almost 45 percent until a year or two before the 1998 elec-tion. Figure 3 also shows a counterfactual trajectory. The hollow dots are predic-tions under an assumption that the coefficients for the Venezuela-specific, post-1993 changes were zero. Recall that we focus only on countries that are sufficientlysimilar to Venezuela as comparison units—that is, Latin American and Caribbeannet oil exporters—and our difference-in-differences models control for all observ-able and unobservable country-specific and time-invariant factors, year-specific and



country-invariant (that is, region-specific) factors, and country-specific trends (intwo functional forms). Therefore, we interpret these additional dots as showing theGini coefficients in Venezuela if there were no Venezuela-specific, systematic changeafter 1993 (i.e., when b1 = b2 = 0).

19 The gap between these factual and counterfac-tual trends represents our estimate of the treatment effects. Specifically, in figure 3,the average effect during the five years after 1993 (i.e., 1994 to 1998) is 4.71 per-centage points.20

DISCUSSION

Strictly speaking, the results in table 1 and figure 3 show only that something hap-pened in 1993 to change Venezuela’s trajectory of economic inequality. Our quali-tative analysis suggests that the abolishment of compulsory voting was the key treat-ment, but we want to rule out other potential explanations. Another importantquestion is whether or not the increase in income inequality was an intended (orexpected) consequence.


Table 1. The Regression Results, Venezuela

Constant T1it T2it H0: b1 = b2 = 0_________ _______ _______ ________________Period Trend b

^0 b

^1 b

^2 F P N

1978–1998 Linear 41.73*** −1.76 0.49 0.18 0.839 127(1.57) (2.86) (0.79)

Quad. 37.50*** 2.17 3.49*** 11.79 0.000 127(1.31) (1.97) (0.91)

1983–1998 Linear 39.29*** 1.09 1.21* 3.74 0.029 102(1.34) (2.22) (0.65)

Quad. 37.92*** 1.94 2.90** 5.09 0.009 102(1.19) (1.65) (1.15)

1988–1998 Linear 38.30*** 2.23 1.65** 5.34 0.008 76(1.19) (1.77) (0.70)

Quad. 38.29*** 2.23 1.69 2.59 0.088 76(1.03) (1.51) (1.80)

*** p < 0.01, ** p < 0.05, * p < 0.10 (two-sided)Note: Two models are estimated for each period of investigation. Each model includes country-specific fixed effects, year-specific fixed effects, and country-specific linear or quadratic trend vari-ables. The base category (for the constant term) is the Gini coefficient in Venezuela in 1993. Thefirst treatment variable (T1it) is the average change in the outcome variable in Venezuela after 1993(exclusive). The second treatment variable (T2it) is the annual increase in the outcome variable inVenezuela after 1993 (exclusive). The null hypothesis is that the coefficients for these two treat-ment variables are jointly zero (H0: b1 = b2 = 0). The numbers in parentheses are standard errors.


Placebo Tests

The comparison set of countries was selected to match Venezuela’s social, economic,regional, and political context. Yet some shared factors might be particularly impor-tant to understand how elections affect inequality. For example, perhaps trends inworldwide oil markets fostered sharp increases in inequality among heavily oil-dependent economies after 1993, or electoral rules other than compulsory votingcontribute to inequality. We conducted placebo tests to explore these possibilities.In the first, we replicated the difference-in-differences analysis reported in table 1for Trinidad and Tobago, the country in our comparison set for which oil exportsas a share of GDP are closest to Venezuela’s. The results show that in none of themodels can we reject (or even come close to rejecting) the null hypothesis of nostructural break in 1993 for Trinidad and Tobago. Thus, we do not find evidencethat 1993 was a pivotal year for the region’s second most oil-dependent country.

Our second placebo test builds on the fact that the end of compulsory votingin Venezuela coincided with the shift from pure PR elections for the legislature to amixed-member proportional system. Our data include another country that imple-mented precisely the same reform during the time period under examination here.Bolivia had previously elected its Chamber of Deputies by proportional representa-


Note: The height of each gray bar indicates the average multiply imputed Gini coefficient inVenezuela. The solid dots are predicted values based on regression analysis (see table 1, 1983–1998, Linear). The hollow dots are predictions under an assumption of no structural break inVenezuela in 1993 (i.e., when b1 = b2 = 0)

Figure 3. The Regression Results, Venezuela


tion in department-level districts.21 In 1994, Bolivia adopted a mixed-member pro-portional system, and held the first election under the new system in 1997. Anumber of other countries adopted mixed-member systems combining SMD andPR competition during the 1990s, including New Zealand, Italy, Japan, Russia, andHungary. Bolivia’s reform is the most closely analogous to Venezuela’s insofar asboth countries moved from pure, closed-list PR systems with regional districts tomixed-member compensatory systems.

In this placebo test, the period of investigation is 1989–2002; the year of treat-ment is 1997. The length of the posttreatment period is the same as the one we usein our analysis of the case of Venezuela. Due to data limitation, however, the lengthof the pretreatment period is a bit shorter. Otherwise, we use the same statisticalmodel and the same data source, and we run the same tests. The results show thatnone of the coefficients for the treatment variables is statistically significant, and thep values of the F statistics are very large. Therefore, we again fail to reject the nullhypothesis of no structural break.

To sum up, our difference-in-differences analysis shows a structural break in1993 for inequality in Venezuela, consistent with an explanation based on the end ofcompulsory voting. We replicated that analysis for two regional cousins for whichcompeting explanations might apply. But we find no evidence that oil dependence inthe mid-1990s or the electoral reform from a closed-list PR system to an MMPsystem accounts for the sharp increase in income inequality in Venezuela after 1993.

Intended or UnintendedConsequences

In our effort to trace causal inference, we assume that Venezuela’s intervention, thedecision to abolish compulsory voting, was independent of the outcome we areinterested in here, economic inequality. That is, if the abolition of compulsoryvoting were part of a broader effort to alter redistributive policies that shape eco-nomic inequality, then the counterfactual case would not provide an appropriatepoint of comparison.

To determine whether this presents a problem, we searched the archival recordfor evidence on what forces drove Venezuela’s electoral reform. Deliberations overelectoral reform in Venezuela in the late 1980s and early 1990s were extensive andinvolved a diverse array of actors, including social scientists, constitutional lawscholars, and politicians from parties across the ideological spectrum. Was thepotential impact of eliminating compulsory voting on economic inequality centralto that debate?

As far back as the 1970s, academic observers of Venezuelan politics appeared torecognize the logic of the redistribution hypothesis when considering the potentialeffects of changes in turnout. Writing during the period of full enforcement of com-pulsory voting and highest turnout, Baloyra and Martz noted, “Electoral demobi-lization would introduce socioeconomic distinctions in voter turnout” (1979, 71).A decade later, however, when debate over electoral reform was proceeding in



earnest, the focus of discussion had shifted to the legitimacy of Venezuela’s repre-sentative institutions.

The single largest source of archival materials on Venezuelan electoral reform isthe Presidential Commission on the Reform of the State (COPRE). Drawing onacademics, politicians, party functionaries, and civil society groups, COPRE pro-duced dozens of reports and compilations that reflect an array of viewpoints on statereform during the years leading up to the end of compulsory voting.22 AmongCOPRE’s list of reports, we identified 11 volumes that address subjects of electoralreform and citizen participation. Carefully reviewing those, we found no discussionof the prospect that ending compulsory voting would affect political support forprogressive redistribution in the Venezuelan electorate. We also reviewed publica-tions on electoral reform proposals from Venezuela’s Consejo Supremo Electoralfrom the same period (Rosales 1986; Zambrano 1989), as well as assorted other aca-demic publications, and similarly found no discussion of the redistribution hypoth-esis associated with compulsory voting.

Although we cannot know with certainty, or document comprehensively, theimpetus for the abolition of compulsory voting in Venezuela, we find no evidencethat the reform was part of a broader set of forces pushing against economic equal-ity. Those engaged in the reform debate at the time and in the immediate aftermathdid not focus on any socioeconomic bias in nonvoting. Indeed, the end of the votoobligatorio was part of a larger wave of electoral reforms that were pitched as egali-tarian overall—empowering ordinary citizens relative to party leaders.

CONCLUSIONS

Given the subsequent rise of Hugo Chávez, any argument that the ideological loca-tion of Venezuela’s median voter shifted to the right in the 1990s might appear per-plexing. We emphasize that our claim about the shifting composition Venezuela’selectorate and the subsequent policy implications is limited to the initial effect ofabolishing compulsory voting in the early 1990s. We do not argue that the effect ofabolishing compulsory voting should persist for a long period and be robust to anyposttreatment political and economic change. Indeed, the policies that followed andtheir effects on the poorest Venezuelans might have pushed the electoral center ofgravity back to the left by directly changing voter preferences on policy and howthose preferences mapped onto candidate choice. Yet we urge caution about pushingsuch an interpretation too far, partly to resist the temptation of perfect hindsight.

We know, retrospectively, that Chávez became the icon of Latin America’snew left, and we know about the redistributive policies he eventually pursuedunder the banner of twenty-first-century socialism (Penfold-Becerra 2007). Butmuch of that was far from clear when Chávez was initially elected, and evenbeyond. Drawing on a national survey taken just a couple of weeks before the 1998election, Weyland (2003) found that respondents’ economic class provided noleverage on their intention to vote for Chávez. Lupu (2010) found that class had aweak effect on retrospective reports of voting for Chávez as opposed to his main



opponent, and that even that effect disappeared once responses from nonvoterswere included in the sample. In short, it might appear that Chávez’s electionmarked a dramatic pivot to the left in Venezuelan politics, but neither the scale ofthe shift nor the intentions of Venezuelan voters were anywhere near so apparentat the time (Zechmeister 2015).

One might also ask why Chávez did not reintroduce compulsory voting whenhe overhauled Venezuela’s institutional structure in 1999–2000. Although wecannot divine his intentions, Chávez might have pursued an alternative tack, strate-gic polarization of Venezuelan politics, toward an effect similar to that of compul-sory voting. Data from across Latin America suggest that party system polarization,like compulsory voting, can mitigate socioeconomic bias in voter turnout whileretaining the flexibility to demobilize some constituencies while mobilizing others(Corrales and Penfold 2007; Carlin and Love 2015). There is evidence that Chávezpreferred rules amenable to selective, rather than universal, mobilization (Hawkinsand Hansen 2006; Hawkins 2010; Albertus 2016). Still, recognizing that the polit-ical environment in Venezuela was turbulent at the time of the electoral reform andwell after, we interpret our central result narrowly, focusing on the shift in the com-position of Venezuela’s electorate in 1993 and the electoral and policy results thatfollowed in subsequent years before the rise of Chávez.

With regard to compulsory voting more generally, however, we emphasize thatmatters of economic redistribution belong front and center. Debates over compul-sory voting are ongoing in a variety of countries, but discussion of the redistributiontheory, which Lijphart forcefully advanced in 1996, is often muted. Colombiarecently entertained the idea of adopting compulsory voting after not having doneso in its nearly two-hundred-year history. Yet a sustained evaluation of the reform’svirtues and drawbacks does not address economic redistribution (Ungar 2011).

A recent Australian state government report on a proposal to end compulsoryvoting lists arguments in favor and against, but it does not mention potential redis-tributive consequences (Queensland Department of Justice and Attorney General2013, 35). The Venezuelan results suggest that from a normative perspective, ques-tions of inequality and redistribution belong at the center of debates over compul-sory voting. Ending compulsory voting, and the subsequent drop-off in electoralparticipation, contributed to increasing economic inequality in the 1990s abovelevels Venezuelans would otherwise have experienced.

NOTES

We thank Aaron Watanabe and Yon Soo Park for research assistance; and AmandaDriscoll, Damarys Canache, and José Enrique Molina for making data available. For helpfulcomments, we thank seminar participants at Dartmouth College; Harvard University; theAnnual Workshop on the Frontiers of Statistical Analysis and Formal Theory of Political Sci-ence (Tokyo, 2014); the Workshop on Citizens, Parties, and Electoral Contexts (Montreal,2014); the 2014 Annual Meeting of the American Political Science Association; and DamianBol, Stephen Brooks, Anthony Fowler, Don Green, Arend Lijphart, and Brendan Nyhan.The order of authors is alphabetical and does not reflect relative contributions.



1. Chong and Olivera (2008) estimate the impact of compulsory voting on incomeinequality. Most of their estimates are based on cross-national regressions, but they also usequestionable instrumental variables for robustness tests. Studies using the cross-national dataconfront another problem in that their treatment variable—whether a country has a compul-sory voting system or not—is causally prior to almost all variables included in their models,because most countries that have compulsory voting introduced it many decades ago. There-fore, their control variables (or exogenous variables, in their two-stage least square regressions)are posttreatment variables, the inclusion of which can introduce bias in causal inference(Rosenbaum 1984).

2. In more recent cross-national studies, however, scholars have reached competingconclusions on whether compulsory voting mitigates stratification of participation by educa-tion (Gallego 2010; Quintelier et al. 2011).

3. We do not use the word positive to imply any normative judgment but rather asimple positive correlation between wealth and voting.

4. Franklin (1999) and Kasara and Suryanarayan (2015) question the prevalence ofpositive turnout bias across nations. Our preliminary analysis, using the Comparative Studiesof Electoral Systems and AmericasBarometer by the Latin American Public Opinion Project(LAPOP), however, supports the traditional view that positive bias is the norm cross-nation-ally and its inverse is extremely rare.

5. In the most recent study, Cepaluni and Hidalgo (2016) note that some sanctionsfor nonvoting, like obstacles to international travel or university enrollment, may hit the richharder than the poor. Sanctions that weigh more heavily on lower socioeconomic classes, bycontrast, such as restrictions on public-sector employment, should bias participation towardmore advantaged groups. The evidence we gathered from Venezuela is consistent with theconventional wisdom that compulsory voting reduces socioeconomic bias, but how sanctionsoperate on individuals across different classes is a promising field of inquiry that warrantsmore attention.

6. We do not require a stronger assumption that governments accurately implementthe preferred policy of the median voter.

7. A shift from voluntary to compulsory voting is expected to produce the oppositeeffect at each link of the causal chain.

8. Language describing voting as a duty remained in the constitution until the prom-ulgation of the new charter in 1999. The elimination of any legal sanctions from 1993 on,however, marks that year as the end of compulsory voting. We thank José Enrique Molina(personal communication, January 21, 2013) for this account of the subtle changes in the dejure and de facto status of compulsory voting in Venezuela over time.

9. Unfortunately, the 1993 contest is the first Venezuelan election included in Bakerand Greene’s data, so we cannot use their index to measure change in the median party from1988 to 1993. Coppedge (1998) provides an index of ideology by blocs (secular left, Chris-tian left, secular center-left, etc.) rather than by parties, which suggests only a modest shiftrightward between 1988 and 1993. But Coppedge’s data are based on legislative, not presi-dential, election results. The structures of competition in the 1993 presidential and legisla-tive races were fundamentally different. Most notably, Caldera won 31 percent of the pres-idential vote whereas his Convergencia coalition won only 14 percent in the legislativecontest.

10. The data source for the government share as the percentage of GDP is Feenstra etal. 2013. The data sources of the Gini coefficients and their uncertainty estimates are Solt2009, 2013.



11. Without the randomization of a treatment variable across units, making causalinference is always difficult in observations. We do not agree with an extreme claim thatemphasizes the invalidity of all observational studies. We acknowledge that our analysis isbased on a set of assumptions, which we make clear as much as possible in this section.

12. See Card and Krueger 1994 for a landmark example of such a design to studydownstream effects of a policy change undertaken by a single state.

13. Another noticeable feature of the SWIID dataset is that it includes one hundredestimates of the Gini coefficient for each country in each year. With the one hundred multi-ply imputed estimates for each country in each year, we can obtain not only a point estimate(i.e., the average of multiply imputed values) but also an interval estimate of inequality.

14. Suriname was also a net oil exporter, but data on income inequality are not availablefor the time period under analysis. Data on oil exports are from Teorell et al. 2013.

15. There is a newer, nonparametric approach called the synthetic control method(Abadie et al. 2010, 2015; Abadie and Gardeazabal 2003). We prefer the traditional approachbased on parametric regression, mainly because it is difficult to account for the uncertaintyestimates of income inequality in the synthetic control method. In our preliminary research,we used the averages of one hundred multiply imputed estimates of income inequality as theoutcome variable (see note 13), under a strong assumption that they were observed facts with-out uncertainty, and estimated the impacts of the intervention in 1993 on Venezuela’sincome inequality using the synthetic control method. The results are essentially similar towhat we report here.

16. The results are largely consistent, which suggests that they are not idiosyncratic tothe choice of model specification.

17. We also undertook permutation tests. For each of the countries included in theanalysis, we estimated whether a structural change in the trajectory of income inequality tookplace in 1993. The model we estimated is exactly the same as the one we use for our mainanalysis. The results show that Venezuela was the only case clearly suggesting a structuralchange in 1993. Specifically, of the 36 non-Venezuelan model specifications, F tests suggesta structural break in only three (and only two at the 5 percent level).

18. To be more precise, the gray bars are the averages of multiply imputed SWIID data(see note 13).

19. Specifically, to calculate the counterfactual trend, we subtracted b^1T1it + b

^2T2it from

the predicted value for each observation Y^it.20. To be more precise, the estimated effect in each of the post-1993 years is 1.089 +

1.207 × (Year – 1993). Thus, the five-year average is 1.089 + 1.207 × S1998i=1994(i – 1993)/5 =4.71. (See also note 19.) Note that the estimated effect is slightly different depending on themodel selection.

21. Bolivia’s 9 departments are its main subnational political and administrative units,analogous to Venezuela’s 24 states.

22. COPRE remained in existence until 1999, but its period of greatest activity wasduring the late 1980s and first years of the 1990s (Cuñarro Conde 2004).



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SUPPORTING INFORMATION

For replication data, see the authors’ file on the Harvard Dataverse website: https://dataverse.harvard.edu/dataverse/laps.



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