Buying Informed Voters:New Effects of Information on Voters and Candidates∗

Cesi Cruz Philip Keefer Julien Labonne

April

Abstract

A theoretical model and two experiments in the Philippines show that informationabout the mere existence of government programs influences both voter and candidatebehavior. Theory predicts that incumbents shirk when voters are unaware of programs.Consistent with this, in the survey experiment, information indicating the availability ofmunicipal development funds significantly reduces support for incumbent mayors. Thefield experiment distributed similar information to voters prior to municipal elections,with the full knowledge of candidates. Incumbent mayors increased vote buying in treat-ment areas to counteract the decrease in voter support. Effects were strongest in villageswith fewer incumbent-provided public goods.

JEL Code: D, PKeywords: Political Economy, Vote Buying, Information, Elections

∗Cruz: University of British Columbia (cesi.cruz@ubc.ca). Keefer: Inter-American Development Bank(pkeefer@iadb.org). Labonne: University of Oxford (julien.labonne@bsg.ox.ac.uk). This project would nothave been possible without the support and cooperation of PPCRV volunteers in Ilocos Norte and IlocosSur. We are grateful to Michael Davidson for excellent research assistance and to Prudenciano Gordoncilloand the UPLB team for collecting the data. We thank Marcel Fafchamps, Clement Imbert, Pablo Querubin,Simon Quinn and two anonymous reviewers for comments on the pre-analysis plan. Pablo Querubin graciouslyshared his precinct-level data from the elections with us. We thank Daron Acemoglu, Michael Callen,Michael Davidson, Jamie Druckman, Chad Kiewiet De Jonge, Andrew Foster, James Fenske, Gyung-Ho Jeong,Chris Kam, Marko Klasnja, Arthur Lupia, Pablo Querubin, Erin Troland, Lily Tsai, and Dean Yang, aswell as conference and seminar participants at ABCDE , Bilkent University, George Mason University,MPSA , Stanford University, University of British Columbia, University of Copenhagen, University ofGothenburg, University of Michigan, University of Oxford, University of Washington, World Bank KnowledgeHub in Kuala Lumpur, and Yale University for comments. We are grateful for funding from the ResearchSupport Budget of the World Bank. The project received ethics approval from the University of OxfordEconomics Department (Econ DREC Ref. No. /). The opinions and conclusions expressed here arethose of the authors and not those of the World Bank or the Inter-American Development Bank.

In many developing countries, incumbents engage in clientelistic practices rather than pro-viding public goods. One explanation for this equilibrium is information asymmetry betweenvoters and politicians: politicians have no incentive to provide public goods in political en-vironments where voters are unable to assess or reward their performance (see, e.g., Besleyand Burgess ). Consequently, politicians have incentives to pursue clientelism insteadof campaigning on policies and promises (see, e.g., Keefer and Vlaicu ). We make twocontributions to the large literature on this issue. First, we show that voters’ ignorance goesbeyond their ability to observe politician effort on their behalf. It extends to a lack of knowl-edge about the very policy instruments on which politicians could exert effort. Second, wetake advantage of our ability, rare in the literature, to monitor how politicians react to in-formation shocks. This allows us to propose an alternative reason for the seemingly modestor mixed effects of interventions that inform voters about politician characteristics and effort:politicians can counteract the electoral effects of information shocks in ways that researchersmay be unable to observe.

We begin with a model of retrospective voting in which voters have incomplete informationabout what politicians can do for them. Incumbents have limited incentives to provide publicgoods because voters do not know that incumbents have resources to provide them. Voterswho are informed that these resources exist are consequently disappointed by incumbents’performance and reduce their electoral support for them. Incumbents, however, react to voterdisappointment by buying additional votes, thereby offsetting the electoral consequences ofthe information shock.

A novel research design combining both survey and field experiments allows us to test thesepredictions, and in particular to track both the direct voter effects and subsequent politicianresponse to an information shock. We use data from the Philippines, where municipalitiesare responsible for implementing public goods using a large fund provided by the centralgovernment, the Local Development Fund (LDF).

The survey experiment allows us to establish the direct negative effects on support for theincumbent of information about the existence of the LDF. Treated respondents received a flyerinformation about the LDF. At the end of the survey, we asked all respondents whether theywould support the incumbent in the next election. Respondents who received the flyer weresignificantly less likely to report that they would support the incumbent in the next election.

Second, to capture incumbent response, we implemented a field experiment in villagesin municipalities ahead of the May municipal elections. Voters in randomly selectedvillages received a flyer with information about the existence and scope of the LDF. To increasethe salience of the flyer for both candidates and voters, the flyer also included candidates’intended allocations out of the LDF. Treated voters are more knowledgeable and incumbentsbought more votes among treated voters prior to the election. Consistent with the theory, theintervention had no effect on either turnout or incumbent vote share.

Third, just as the theory suggests, the effects of the information – both in the surveyand field experiments - are greatest in villages where respondents report fewer municipality-provided infrastructure projects. Those are precisely the villages where voters have greatestreason to be disappointed in the incumbent’s performance.

This study, and research with a different focus by Bidwell et al. () and Banerjee et al.(), are the first to examine the reaction of politicians to information programs directed atvoters. Understanding these reactions is key, since the electoral effects of voter information aremediated by politician responses to it. Voters who find out about a program that incumbentscould have accessed for the provision of public goods, but didn’t, will reduce support unlessthe incumbent is able to respond to voter disappointment with greater vote buying.

In addition, the information we provide is both new to empirical research and central tothe analysis of elections. Typically, analyses of electoral competition assume that voters knowthe policy instruments of government and politician intentions regarding those policies. Weshow that this assumption does not necessarily hold and that the voter’s challenge is not onlyto assess whether governments have implemented the policies they prefer, but even to knowwhat those policies are in the first place (see, e.g., Banerjee et al. ; Cruz and Schneider; Labonne ).

This paper extends the literature on information and electoral accountability, by focus-ing precisely on a previously unexplored information asymmetry - knowledge of the existenceof government programs - and by examining politician reactions to information shocks. Im-pressive research has investigated the effects of informing voters about past performance orpersonal attributes of incumbent politicians, including their corrupt behavior. Among morerecent contributions, Kendall et al. (), Ferraz and Finan (), Gottlieb () andBanerjee et al. () find significant electoral effects while Humphreys and Weinstein ();Chong et al. () and Larreguy et al. () do not. Dunning et al. (forthcoming) re-port on the results of a large research effort to conduct similar information interventions indifferent countries, with mixed results. One potential explanation for these mixed results isthat researchers could not easily observe effects on candidate behavior, which Pande ()targeted as a priority area of future research.

Bidwell et al. () and Banerjee et al. () are the only other research effort withwhich we are familiar that has answered the call in Pande () for more research on politicianreactions to electoral interventions. Bidwell et al. () examines the effects of voter exposureto candidate debates in Sierra Leone. Treated voters expressed policy preferences more aligned

The treatment closest to ours is Gottlieb’s () experiment providing voters with information aboutlocal government capacity and responsibilities, although hers differs in also providing information about therelative performance of candidates. She finds that treated voters are more likely to sanction poor performers.Chong et al. () do not look at vote buying, but like us distributed flyers that implicitly informed votersof the existence of a public infrastructure program of which they had been largely unaware. However, theflyers also contained additional performance information that is absent from our treatment (the percentage ofprogram funds spent; the percentage spent allocated to the poor; or the percentage of program spending thatsuffered from accounting irregularities).

with those of their favorite candidate and were more likely to vote for the candidate whoperformed best during the debates. Debates significantly increased reported vote buying bythe third party candidates, from less than one percent of voters to . percent, an effect drivenby the most closely contested debates. It had no effect on vote buying by candidates from thetwo main parties. Banerjee et al. () organises a voter awareness campaign that informedvoters of their village leaders’ role in implementing a large scale public works program inIndia. As a result of the intervention, worse-performing incumbents decided not to run andcandidates from disadvantaged groups. Those effects persist until the next village election.

The paper also contributes to the literature on vote buying, the pre-electoral provision ofgifts of goods or money aimed at persuading recipients to vote in a particular way, to turn outto vote, or not to vote at all (Hicken, ; Schaffer and Schedler, ; Nichter, ). Thepractice is pervasive and can entail large transfers to voters. In our control group, percentof households report vote buying. Numerous papers examine the effects on vote buying ofdiverse information treatments (Hicken, ; Vicente, ; Aker et al., ; Fujiwara andWantchekon, ), but none examine the impact on vote buying of voters’ information aboutwhat politicians can do for them.

Theoretically, the focus here on voter information complements work that links pre-electoral vote buying to the possibility that politicians will renege on their campaign promises(Keefer and Vlaicu, ). The tradeoffs we document between vote buying and the provisionof public services are also consistent with Khemani’s () findings in the Philippines.

In the remainder of the paper, Section presents a retrospective voting model of politicalcompetition where candidates cannot make credible pre-electoral promises. Section describesmunicipal elections in the Philippines. Section details the results of a survey experimentthat isolates the effect of our information treatment on voter support for politicians, absenta politician response. Section presents the direct effects of the information interventionboth on voters and the subsequent candidate response, as well as evidence for the additionaltestable mechanisms and model assumptions.

Information, Government Resources, and Vote Buying

The literature focuses on the need for information in order to assess politician performance:what politicians have previously done; and what politicians propose to do in the future.

Across the countries surveyed in the - wave of the Afrobarometer survey, percent of morethan , respondents reported that they had been offered a gift in the last election. Brusco et al. ()surveyed nearly , respondents in three Argentine provinces three months after the October elections.Forty-four percent of respondents said that parties had distributed food, clothing and other items to homes intheir neighborhoods.

Another large literature, that we do not address, examines the enforcement of vote buying transactions,such as party machines and social networks (Brusco et al., ; Cruz, ) or norms of reciprocity (Finanand Schechter, ), and on the extent of leakage-voters who do not necessarily vote for the politicians whopay them, as in Schaffer and Schedler ().

However, before voters can make use of information to assess politician performance, they needto know what politicians could potentially do for them in the first place. In many developingcountries, voters are unaware of this fundamental piece of information. This is especiallyproblematic in decentralized settings, where voters face multiple government actors at differentlevels and may be ignorant of the responsibilities and resources of each. Local politicians takeadvantage of these low-information political environments and benefit electorally from centralgovernment programs (see, e.g., Cruz and Schneider ; Labonne ). Nevertheless, theincomplete information of voters regarding what governments can do for them has receivedlittle attention (Banerjee et al., ). We argue that when voters are informed that localgovernments can deliver benefits that voters previously thought they could not, they will bedisappointed in the performance of incumbent mayors and reduce support for them.

The effects of interventions that reduce this information asymmetry depend on politicianreactions to it. In the long run, reducing the asymmetry can reverse politician underperfor-mance with respect to public good provision. However, in the short run, when politicians havelittle ability to change public good provision, they may respond with increased vote buying.Short run reactions matter, since many interventions take the form of one-shot treatmentsvery close to the elections. Politicians therefore react with strategies that are more readilyimplemented in a short period of time and may be difficult to observe, such as clientelism.Empirical studies of the effects of information on electoral outcomes can lead to null resultsor understated effects when they are unable to account for politician responses.

We develop a formal model to examine the effects of a shock to voter information aboutwhat government can do for citizens. Our specific intervention consists of a flyer that informedvoters of the existence of a key government program to fund local development projects. Hence,we formalize the argument that, taking advantage of voter ignorance of the program, incum-bents shirked in implementing it, leading to voter disappointment when voter informationincreased. To offset this disappointment, incumbents engaged in greater vote buying prior tothe election.

. Program information and retrospective voting

Reflecting the inability of mayoral candidates to make credible commitments regarding post-electoral policies, we adopt a retrospective voting framework: voters establish a performancethreshold for incumbents and vote for or against the incumbent depending on whether theincumbent has met the threshold. If the threshold is too high, incumbents make no effortto deliver benefits to voters and, instead, maximize private rent-seeking. If the threshold istoo low, voters extract fewer benefits from the incumbent than they could have. Assumingthat voters can spontaneously coordinate on this threshold, as in Ferejohn () and Perssonand Tabellini (), their challenge in setting the threshold is uncertainty about the welfarethat the incumbent could have potentially delivered. Voters’ incomplete information makes

it difficult for them to distinguish incumbent shirking from an unfavorable state of the worldthat would prevent any incumbent from improving welfare.

This analytical approach is consistent with two key features of politics in many developingcountries, and mayoral elections in the Philippines in particular. First, political competitiondoes not center on policy promises, which are not credible. Hence challengers do not matter,and voters base their decisions only on whether incumbent performance meets the thresholdvoters have set. Second, mayors are the dominant decision makers in municipal governmentand voters should hold mayors accountable for their spending out of the Local DevelopmentFund.

. Basic Set-Up

There are N arbitrarily small groups of voters indexed by i. Incumbent mayors can spendmoney either on public goods such as infrastructure, g, or on direct transfers to voters, fi.Since subnational governments in many countries, including the Philippines, rely on transfersfrom the central government, the government budget is exogenous and given by M . As in thecanonical retrospective voting model (e.g., Persson and Tabellini , pp - ), publicgoods deliver welfare H (g) to each voter, while transfers deliver welfare equal to the amountof transfers that the voter receives. The cost of all transfers received by voters is

∑fi.

The cost parameter governing public good provision is θ̄ and total costs of providing publicgoods are therefore θ̄g. The cost is higher when there are restrictions on the type of publicgoods that can be purchased, when the costs of inputs and construction are high, or when thebureaucracy is incompetent. As long as the costs θ̄ are not too high, government decisionsto spend more on local public infrastructure delivers greater welfare to voters per peso ofspending than do direct transfers.

Mayors choose direct transfers and public good spending to maximize their pecuniaryrents, r = M −

∑N fi − θ̄g, and the non-pecuniary rents from being re-elected, R:

M −∑N

fi − θ̄g + pR

where p is the probability of re-election. In the event that they do not expect to be re-elected,they set g = f = 0 and take as pecuniary rents the entire budget.

The welfare of voters in group i is given by ω = fi +H (g). Voters prefer that the mayordedicates the municipal budget to public goods until Hg (g) = θ̄N , the Samuelsonian conditionfor public good provision, and then to distribute any remaining budget in the form of transfers.

Challengers are absent from retrospective voting models, since the key parameter affecting voter choiceis incumbent performance, which challengers cannot affect. In principle, challengers could exploit negativeinformation shocks about incumbent performance by increasing vote buying in areas affected by the shock.Such challenger reactions are uninteresting, however, since they are driven by the same mechanism that weare considering and operate in the same direction.

We add two features to this standard set-up. First, we introduce an information shockthat affects voter knowledge of what government can do for them. In the field experiment,voters receive information about the existence of a government program about which theywere previously ignorant. Such an information shock can be modeled in two equivalent ways.First, voters could be uninformed about the government budget constraint. Second, voterscould be ignorant about how much it costs government to procure projects. An informationshock that reveals that government can do more for voters than they thought would, in thefirst case, simply tell them that the government has more money than voters thought. Inthe second case, it would tell that that the government can implement projects more cheaplythan voters thought. We adopt the second approach, which yields a continuous relationshipbetween the amount that actual costs exceed expected costs and the probability of supportingthe incumbent.

Specifically, voters are uncertain about the costs to the incumbent of providing them withpublic goods. Just before the election, each voter’s beliefs about the costs of producing publicgoods are drawn from a uniform distribution given by θi ∼ [1, 2θc − 1], θc > 1. Incumbentsknow this distribution, but not the beliefs of individual voters. The median belief about theincumbent’s costs of producing public goods is given by the cost parameter θc. The ability toproduce is never less than one - it can never cost less than g to produce g.

An intervention that changes voters’ beliefs about what government can do more for themis equivalent to an unexpected shock that shifts this distribution for a randomly-selectedfraction δ of all voters, δ ≤ 1. Incumbents know which voters are subject to the shock, butbeyond that only know that the distribution of beliefs about the costs of producing publicgoods follows θ′i ∼ [1, 2θ′c − 1], where θ′c = θc+k

(θ̄ − θc

), and the shock parameter k ∼ [−1, 1].

Recalling that citizens do not know θ̄, the true cost of producing public goods, the effect of theinformation shock reflects the assumption that the more accurate are the beliefs θc of citizensregarding the costs of public good provision, the less they change in the event of a shock. Thisis plausible in general, and specifically consistent with our experimental intervention, since weprovided voters with the “true” ability of politicians to provide public goods; those voters whoknew this already were therefore unaffected by the intervention.

The information shock in our field experiment, and in the model here, is unanticipated.Hence, incumbents do not take it into account when deciding on public goods.

The second feature of the model that we add to the standard set-up is to recognize that formost public goods, spending takes time to implement before voters perceive a change in theirwelfare. Mayors must therefore decide to spend money on public goods early in their terms

The first approach generates the same general conclusions, but less elegantly, since we observe changesin behavior only for corner solutions, when the difference between the actual and expected budget exceeds acertain threshold.

As discussed in more detail below, δ is approximately . percent in the case of our field experiment.We abstract from anticipated information shocks. Their inclusion would complicate the analysis, but not

change the key results.

(Robinson and Torvik, ). Transfers, however, can be implemented quickly, even at the endof the mayor’s term and right before the next election. Mayors have two opportunities, then,to make budget decisions. Earlier in their tenure, they can decide to supply public goods ortransfers (though, for any expenditure amount, public goods deliver greater welfare to voters).Late in their tenure, they can only deliver transfers. This accurately reflects the limitationson incumbents’ ability to react to information shocks in the weeks before an election.

As usual in retrospective voting models, citizens coordinate on a voting rule that is condi-tional on their beliefs about the costs of public good production just before the election, afterthe mayor has provided public goods. At the beginning of the mayor’s term, voters establishthe rule that, given their individual draw from the distribution of potential pre-electoral beliefsabout the costs of public good production, θ′i , they will support the incumbent who meetsthe performance threshold ω̄i ≥ H (gθ′), where gθ′ is determined implicitly by Hg (gθ′) =

2θ′iN .

The stages of the game are the following:

. Incumbents and voters observe the distribution of beliefs about the costs of public goodprovision, θi ∼ [1, 2θc − 1], that voters will have before the election.

. Voters coordinate on a voting rule ω̂ = ω (gi), where gi is given by Hg (gi) = 2θiN .

. Incumbents choose the level of public good provision g.

. A randomly-selected subset of all voters δ ≤ 1 are subject to an unanticipated shock kto the distribution of their beliefs about the costs of producing public goods, such thatfor these voters θ′i ∼ [1, 2θ′c − 1], where θ′c = θc + k

(θ̄ − θc

), k ∼ [−1, 1].

. Incumbents choose the level of spending on transfers to voters.

. Voters’ individual beliefs about the costs of public good provision are revealed to them.

. The election takes place.

Proposition establishes the equilibrium level of public good provision. The remainder of theanalysis then describes the conditions under which vote buying takes place, the amount ofvote buying, and the voters targeted for it.

In the usual retrospective voting model, both an economic shock and government policy affect voter welfare;voters do not observe either, but take the distribution of the shock into account when setting a performancethreshold for the incumbent. The incumbent observes the shock and makes policy. Here, neither politiciansnor voters anticipate the shock that will inform voters about politician ability; and politicians do not observethe shock before they set public goods provision. Since politicians cannot exploit an information asymmetrybetween themselves and voters, as in the canonical model of retrospective voting, voters can do no better thanto require politicians to meet the performance threshold that is indicated by the revelation of θ′, voters’ bestinformation about the true efficiency of public good provision.

When voters observe public good spending g, from the participation constraint of the incumbent they caninfer an upper limit on the cost of providing public goods, θ ≤ R

g. The voters who believed that the cost was

higher than this immediately update their beliefs about costs. However, this updating does not change theirvoting behavior, since incumbent spending that satisfies the performance threshold of voters who believe thecosts were θ by necessity satisfies those who believe the costs were higher, and who set a lower performancethreshold.

Proposition Incumbents set public good provision to meet the expected performance thresh-old given the voting rule, ω̄ = H (gθc), where public good provision is given by Hg (gθc) =

2θcN .

Proof : See online appendix.

Lemma confirms that unanticipated information shocks that change voter expectationsabout the costs of providing public goods affect voter support for the incumbent.

Lemma After a positive unanticipated information shock, k(θ̄ − θc

)> 0, a fraction of

voters δ believe that the costs of providing public goods are higher than they previously believedand the public goods provided by the incumbent meet the performance threshold of more thanhalf of the voters. After a negative unanticipated information shock, k

(θ̄ − θc

)< 0, a fraction

of voters δ believe the costs are lower than previously believed and public good provision meetsthe threshold of less than half of the voters.

Proof : See online appendix.

Proposition describes the incumbent response to an information shock. If the shock isadverse (it tells voters that it is less expensive to provide public goods than they anticipated),incumbents increase pre-electoral transfers and they target those transfers to those affected bythe shock. This case is particularly relevant to our analysis, since voters in the Philippines aremore likely to under-estimate what local politicians can do for them, and to be disappointedwhen provided accurate information about government programs.

Proposition After a positive unanticipated information shock, k(θ̄ − θc

)> 0, there is no

change in public policy. In the event of a negative unanticipated information shock, incumbentstarget transfers fk = H

(ggθc+k

)− H (gθc) to a fraction α of voters in δ who received the

information shock, where α is given by α∗ = M−θ̄gθc+R+lδfkδfk , l =12

(k(θ̄−θc)

θc+k(θ̄−θc)−1

).

Proof : See online appendix.

Proposition shows that voters who receive more accurate information about the publicgoods the incumbent could have provided raise their performance threshold, in accordancewith the voting rule. Since incumbents cannot adjust the provision of public goods in timefor the election, they respond to the higher threshold by targeting more informed voters with

The prediction that information about municipal resources leads to voter disappointment depends onwhether incumbents have an information advantage, leading voters to systematically underestimate whatincumbents can do for them. This assumption is especially plausible in the Philippines, where journalists aresubject to significant pressure relative to other countries. The Freedom House () report on press freedomrates the Philippines as only partly free. Journalists are the targets of libel suits by local politicians, as wellas harassment and assassinations. According to Campos and Hellman (), voter information at the locallevel is particularly likely to suffer from poor media penetration and reduced media capacity

greater vote buying. This result emerges because public good spending begins substantiallybefore the election, while transfers can be made right before the elections. Evidence from thePhilippines, discussed below, supports these assumptions.

The experiments we report below offer evidence in support of the main predictions of themodel. A survey experiment allows us to measure effects on voter preferences for incumbents,since incumbent reactions to information shocks are precluded by construction. Respondentsexpress lower support for the incumbent when they are informed about the existence of amajor government program. In the field experiment, where incumbents could react, areasthat received a flyer with information about the program exhibited greater vote buying and,therefore, no net change in electoral support for the incumbent.

We also present evidence for ancillary predictions and assumptions of the model. Informa-tion effects are strongest in villages that reported less public good provision in the previousthree years. Treated respondents who report the recent provision of public goods have lessreason to be disappointed in incumbent performance and were correspondingly less likely toexpress lower support for the incumbent, in the survey experiment, or to be targeted for votebuying in the field experiment. In addition, in the retrospective framework employed here,voters care most about incumbent characteristics and performance. We should therefore ob-serve stronger information effects with respect to incumbents than to challengers on voterknowledge of candidates and on candidate vote buying. These stronger effects emerge in thedata.

Context

Our experiments examine the electoral incentives of voters and candidates in mayoral elec-tions in the Philippines. This context has four characteristics that make it ideal to empiri-cally identify the electoral effects of information about the existence of government programs.First, mayors control important public spending programs. The Local Government Codedevolved a number of responsibilities to municipalities, such as responsibility for nutritionprograms (Khemani, ), and transferred a large number of civil servants to them (Llanto,). Mayors exert significant control over how municipal resources are spent (Hutchcroft,). Hence, voters can reasonably attribute the outcomes of municipal programs to themayor, in contrast to alternative research designs that, for example, focus on candidates innational legislative elections. Especially in countries with weak parties, a common characteris-tic of clientelistic democracies such as the Philippines, policy performance or non-performanceis difficult to attribute to any single legislator.

Second, consistent with our focus on an exogenous source of municipal funding, mayorshave little influence over municipal revenues. For the average municipality, fixed transfers fromthe central government pay for percent of municipal spending (Troland, ). Laws gov-erning transfers to municipalities encourage municipalities to allocate percent of transfers

to development projects.Third, mayoral candidates are unable to make credible commitments about their future

policies. Institutionally, Filipino mayors are often viewed as local bosses (Capuno, ; Sidel,) subject to few checks and balances on their decisions regarding municipal budgets andspending. Nor does party membership constrain them: policies and party platforms playlittle role in elections (Hutchcroft and Rocamora, ; Kerkvliet, ). Vote buying andretrospective voting play a significant role in electoral competition under these circumstances.Consistent with this, prior research documents not only that vote buying is pervasive in thePhilippines, but also that Filipino voters use retrospective voting rules when deciding whetherto re-elect the incumbent (Cruz and Schneider, ; Labonne, , ). Hence, thedissemination of information about previously unknown government programs should influencevoter preferences.

Finally, vote buying takes place a few days before the mayoral elections (Cruz, ). Theinformation intervention was consistent with this timing: voters received the flyers in the weekbefore the election. Moreover, ample evidence demonstrates that incumbents routinely adjustthe targeting of vote buying to shocks that occur in the days leading up to the election. Onecampaign staffer for an incumbent mayor described in detail how local brokers immediatelyinform their candidates about village events that might affect the election. Candidates then,with equal rapidity, adjust their vote buying strategies accordingly.

Isolating Information Effects on Politician Support: SurveyExperiment

We seek to test a key prediction that new information about the existence of governmentprograms should reduce voter support for incumbents. Since we also predict that incumbentswill take measures to offset this drop in support prior to the elections, we cannot measuresupport using actual voting behavior. Instead, we conducted a large survey experiment inSeptember in three Philippine municipalities. During the survey, treated respondentswere given the opportunity to study a flyer that described the Local Development Fund. Byconstruction, the survey experiment design precluded a strategic reaction by incumbents. Atthe end of the survey, all respondents received a secret ballot, asking how likely they wereto support the incumbent in the next election. Respondents who received the flyer withinformation about the Local Development Fund were significantly less likely to report thatthey would support the incumbent. This is the first demonstration in the literature that themere revelation of the existence of a government program can reduce support for incumbents.

Example events include not only campaign activities of rival candidates, but also non-partisan activities,such as pre-election surveys, flyer distributions, and voter education campaigns. Consistent with this, just oneday after our teams began to distribute flyers, the PPCRV received their first phone call from a candidateasking for clarification about PPCRV activities in his municipality.

Within each of the three municipalities, randomly-assigned respondents received in-formation on the LDF and randomly-assigned control respondents did not, for a total of respondents. We selected three municipalities where the incumbent was in his/her firstor second term, to avoid incumbents who are ineligible for reelection, and randomly selected villages per municipality. Within each village, the survey team used the village list torandomly select respondents for the survey experiment. Ten of them received the flyer andten did not.

Treated and control respondents are balanced across variables for which we have in-formation: there are no significant differences among them with respect to their length ofresidence in their village; their gender, age, education levels; their household size; whetherthey receive remittances from abroad; whether they benefit from the Philippines conditionalcash transfer program; whether they have asked the mayor or village captain for assistance;and whether they voted in the municipal elections (Table A.).

Towards the end of the interview, treated respondents were then presented with a flyerwith information about the LDF, including the ten categories of spending that could beundertaken under the program. The survey ended with a secret ballot in which respondentsindicated how likely they would be to support the incumbent mayor in the next election.

The secret ballot asked respondents whether they were very likely, likely, neither likely norunlikely, unlikely or very unlikely to support the incumbent in the next election.

Our argument predicts that the information intervention should have led voters who werepreviously ignorant of the Local Development Fund to believe that the incumbent had greatercapacity to provide services than they had previously thought. These respondents would havetherefore raised their performance threshold—their expectations of incumbent performance.To the extent that incumbents had taken advantage of voter ignorance by shirking on theirobligations to deliver LDF-funded projects, some respondents who would have expressed sup-port for the incumbent prior to the information intervention should have been disappointedand instead indicated that they were neutral, unlikely or very unlikely to support the incum-bent. Among respondents who already did not support the incumbent, the higher performancethreshold simply meant that they continued not to support the incumbent. Among respon-dents who already knew of the existence of the Fund, support for the incumbent should havebeen unchanged.

In fact, we find that respondents who received information about the Local DevelopmentFund were significantly less likely to express support for the incumbent. Table indicatesthe percentage of respondents in the treatment and control groups who chose each of theresponse categories. A notably smaller fraction of respondents (six percentage points fewer)said that they were "likely to support the mayor". Correspondingly, a notably larger fraction

A copy of the flyer is available in Figures A. - A.. The translation is available in Table A..Three respondents in the treatment group decided not to answer that question. We get similar results if

we assume that non-response corresponds to individuals who would have responded "very likely".

of respondents in the treatment group (. percentage points more) were neutral.We then classify each respondent as supporting the incumbent (very likely or likely cate-

gories), being neutral or not supporting the incumbent (unlikely or very unlikely categories).Controlling for village fixed effects, treated voters are between seven and eight percentagepoints less likely to express support for the incumbent and approximately . percentagepoints more likely to be neutral (Table ). The magnitude of these effects is large, reducingsupport for the incumbent by percent. Although the results are noisy, all are significantat least at the percent level. In addition, the negative treatment effect on support forthe incumbent is significant at the five percent level when we include individual controls toimprove power.

Respondents who already believed that the incumbent did not meet their performancethreshold (voters who were neutral or unsupportive of the incumbent prior to the survey) didnot change their stance when they were exposed to the information treatment. The increase inneutral voters comes exclusively from the group of respondents who would have been likely tosupport the incumbent in the absence of the information treatment, but who instead becameneutral as a result of hearing about the Local Development Fund.

The survey experiment also yields evidence in support of the mechanism. We asked par-ticipants in the survey experiment to report public investments in their villages that had beenfinanced by the incumbent mayor. Their responses were averaged over each village to createa variable for the number of mayor-funded projects reported by respondents. The originalregression specification examines the effects of the information treatment on support for theincumbent. This specification is supplemented with the interaction of the number of projectsin each village with treatment status (the base effect is captured by the village fixed-effects).In an alternative specification, we control instead for a dummy variable, whether the villageis above or below the median with respect to number of projects and its interaction with thetreatment dummy.

Panels A and B of Table display the results: the negative treatment effect on support forthe incumbent is concentrated in villages where the incumbent provided fewer public goods.

These effects emerge despite the fact that the survey experiment occurred in the middle ofthe electoral cycle, rather than shortly before the election, like the field experiment. This tim-ing gives rise to a possible spurious downward bias in the estimation of the survey experimenttreatment effect. First, elections were less salient, and therefore the treatment less powerful.Second, it would be reasonable for respondents to evaluate incumbents more leniently in themiddle of their term, since they still have time to implement projects, than at the end. Despitethis downward bias, the information treatment had significant effects.

These results are novel in and of themselves. It is well-known that events out of the controlof incumbents, from natural disasters to changes in commodity prices, can significantly affecttheir support. This is the first instance in which research has documented that information

about the simple existence of a public program can depress support for incumbents. This isclosely related to findings by Banerjee et al. () showing the effects of informing voters ofvillage leaders’ responsibilities in implementing a large public employment program in India.It underscores the extent to which basic information about public policy is intertwined withcitizen evaluations of incumbent performance.

Voter Effects and Incumbent Response: Randomized Infor-mation Campaign

Our second major prediction is that citizen exposure to information about the existence ofgovernment spending programs, shortly before an election, will lead to an increase in votebuying among treated citizens and, therefore, no change in electoral support for the incumbent.To test this proposition, we distributed a flyer to all households in randomly selected villagesin the week leading up to the May , mayoral elections ( months before the surveyexperiment). After the elections, we conducted a household survey in treated and controlvillages and used that data, along with administrative data on election results, to test theprediction.

The flyer for the field experiment had the same format as the flyer presented to the respon-dents in the survey experiment. It contained the same information about the Local Devel-opment Fund. However, two circumstances compelled us to include, in addition, statementsfrom all mayoral candidates in the municipality regarding their LDF allocation preferences.

First, our collaborator, a well-regarded non-governmental organization, the Parish PastoralCouncil for Responsible Voting (PPCRV), wanted to increase the electoral salience of policyrelative to vote buying. It therefore preferred an intervention that encouraged candidates toexpress policy preferences and subsequently disseminated those preferences to voters. Second,by introducing the Local Development Fund into the election, we invited a range of possibleresponses from candidates. In particular, although the facts on the ground in the Philippinesindicate that policy statements are neither relevant nor credible, we could not preclude thatcandidates would respond to the flyer with last-minute position-taking on the LDF, and wecould not assume that the position-taking would have no effect on voters. We therefore wantedto control for potential variation across treated households in exposure to candidate statementsregarding their preferences over LDF allocations. To do this, we solicited those statementsdirectly from candidates and included them directly in the flyer. All treated voters thereforereceived the same information about candidates’ allocation preferences.

This additional information introduces potential ambiguities regarding the interpretationof any treatment effect. To offset this ambiguity, we collected information on voter preferencesregarding LDF and are able to show that the distance between candidate and voter allocationpreferences has no influence on either vote buying or vote choice.

In April , we interviewed every candidate for mayor in twelve municipalities in theprovinces of Ilocos Norte and Ilocos Sur, in the northern Philippines. Candidates weretold that the information they provided would be given to randomly-selected villages in theirmunicipality prior to the election. In the course of the interview, we gave each candidate aworksheet with a list of sectors. Candidates were told the average amount that they wouldhave to spend from their local development fund (LDF) and asked to allocate money acrosssectors. To facilitate this decision, candidates received tokens to place on the worksheetand were told that each token represented five percent of the total LDF.

Candidates took the allocation exercise seriously. During the interview, they typicallyspent several minutes to arrange the tokens after considering their allocation.

There are also two quantitative indications of the seriousness of candidate allocations.First, the spending intentions of incumbents were correlated with how they had actuallyallocated their budgets prior to the interviews. Second, in response to one of the surveyquestions, candidates listed three specific projects and programs that they would implementif elected. Candidates consistently allocated a greater share of their proposed budget to thesectors to which these projects and programs belonged (see Figure A.).

Within each target municipality, villages were allocated to treatment and control usinga pairwise matching algorithm. The final sample includes treatment and controlvillages in twelve municipalities (cf. Table A.). The treated and control villages contained percent of all voters in the municipalities, evenly split between treatment and control villages.The remaining percent of voters resided in villages that were not part of the experimentbecause the data to run the matching equilibrium were missing.

PPCRV prepared flyers showing the proposed allocations of all candidates in each mu-nicipality, together with the basic information about the Local Development Fund (LDF), inthe same format as the flyer for the survey experiment. Then, in the week leading up to theelection, PPCRV volunteers distributed the flyers to all households in target villages through

Note that the survey and field experiments were conducted in different regions of the Philippines, sincethe results of one would have been contaminated by exposure to the other.

Candidate names were taken from the official list of the Commission on Elections (COMELEC). Mostcandidates were eager to participate (only one refused), even contacting PPCRV to ask if they would beincluded. Incumbent willingness to participate may appear puzzling, given that one effect of the informationtreatment was to increase incumbent vote buying. In fact, since incumbents knew that the flyer would bedistributed regardless of their participation, their best response to potential voter disappointment and exposureto challenger spending intentions was to be sure that at least their own spending intentions were shared withvoters.

We use budgetary data for the last full fiscal year before the election () and compute the correlationbetween the share of the budget spent on each sector with the share of the budget that the incumbent proposesto spend on the sector. Despite changes in priorities and errors in budget data, the correlation is large, at ..

First, for all potential pairs, the Mahalanobis distance was computed using village-level data on population,number of registered voters, the number of precincts, a rural dummy, turnout in the municipal election andincumbent vote share in the elections. Second, among , randomly selected partitions, the partitionthat minimized the total sum of Mahalanobis distance between villages in the same pairs was selected. Third,within each pair, a village was randomly selected to be allocated to treatment; the other one serving as control.

door-to-door visits. The teams were instructed to visit all households in the village and givethe flyer to the head of household or spouse, and in his or her absence, a voting-age householdmember.

Although candidates were not told which villages would be treated, they had ample ca-pacity to modify their vote buying in response. The flyers were distributed by teams of -PPCRV volunteers who arrived in each village riding in minivans (jeepneys), an event that,within hours, candidates’ brokers and representatives relayed to the candidates. In the Philip-pines, candidates have a wide network of brokers (or liders) across villages, often building onexisting social ties and obligations to family members, employees, tenants and others (Lande,; Fegan, ; Cruz et al., ). These brokers are involved in distributing flyers andposters, coordinating rallies, and assisting with vote buying and other illegal strategies. Theyeven serve as poll watchers on election day itself. Because vote buying is a logistically demand-ing electoral strategy, candidates do their hiring and recruiting months before the election toensure that they have sufficient staff to be able to buy votes during the campaign period.This infrastructure permits them to react quickly when circumstances change, as turned outto be the case with the distribution of the flyer. Hence, we expected that our informationintervention could potentially affect vote buying.

For each household visit, volunteers used a detailed script to introduce themselves andexplain the information contained in the flyers. Visits lasted between and minutes andvolunteers left a copy of the flyer. No households refused the flyers. Neither the flyer nor thescript mentioned vote buying, nor contained any other normative information concerning theelectoral process, reducing concerns related to social desirability bias. A detailed timeline ofthe experiment is available in Table A.. The pre-analysis plan (PAP) was registered withJ-PAL’s hypotheses registry on May , .

The results in Table A. indicate that the village-level variables used to carry out thepairwise matching exercises are well-balanced across the treatment and control groups. Wealso use data from the survey to test if the treatment and control are balanced with respectto household composition, households assets, etc. Out of the village- and household-levelvariables for which we test balance, only exhibit differences that are significant at the percent level. Controlling for these variables does not affect results reported below.

A copy of a flyer is included as Figures A. and A.. The translation is available in Table A..Due to time constraints, there were no additional visits on different days if no voting-age household member

was present on the day of the visit. Our enumerators did not report problems with contacting households withthe flyers.

This is consistent with Stokes et al. (), who argue that candidates give local brokers resources to ensurea certain level of support for the candidate. Brokers retain some of these resources as rents for themselves,but rapidly disburse when they observe an information shock that reduces support for their candidate.

The submitted documents are available at: http://www.povertyactionlab.org/Hypothesis-Registry andhttps://www.socialscienceregistry.org/trials/

This set of results is available in Table A.-A..

. Data

The analysis relies on two main data sources. First, precinct-level election results from theCOMELEC include information on the number of votes obtained by all candidates in themayoral elections. Second, we implemented a household survey in villages in twelvemunicipalities in June . In each village, the team obtained the list of registered voters forthe May elections and randomly selected twelve individuals to be interviewed for a totalsample size of , households. These interviews yielded the key variables that we use in theanalysis. Descriptive statistics are reported in Table .

Occurrence of vote buying The challenges of measuring vote buying are well-known.Measures based on actual observation are rare because vote buying is a private transactionand dispersed both in time (the weeks leading up to the election) and space (not only at thepolling station, but also at people’s homes). Researchers instead rely on survey evidence ofvote buying. The simplest approach, asking people directly about their experience with votebuying, is also the most accurate way to identify treatment effects, as long as the experimentaltreatment does not affect social desirability bias - the reluctance of people to answer questionsabout a potentially delicate subject. In fact, we have no reason to expect that our informationtreatment would affect social desirability bias.

First, the flyer is entirely silent on normative issues in general, and specifically on issuesrelated to electioneering, campaigning and vote buying itself. We demonstrate below that votebuying was no more electorally salient for the treatment than for the control group. Second,even in cases where normative information is present, it need not affect social desirabilitybias. Vicente (), for example, analyzes the effects of an information intervention explicitlydirected at reducing voter acceptance of vote buying in Sao Tome and Principe and finds thateven such an overtly anti-vote buying intervention has no effect on social desirability. Third,social desirability bias associated with vote buying in the Philippines is known to be low. Usinga survey in Isabela, a province near our study area, Cruz () finds that the estimated rateof vote buying using an unmatched count technique are statistically indistinguishable fromthe estimate calculated using the direct question. This suggests that responses to directquestions provide credible estimates of vote buying incidence. Similarly, Khemani () alsouses direct questions to estimate vote buying in research in the same province. Therefore, forthe analysis below, we measure vote buying according to whether respondents reported beingoffered money for their vote during the recent election.

One test for whether our treatment affects social desirability is to ask whether non-responserates are significantly different in the treated and control groups, since reticence may take theform of non-responses instead of false answers. The non-response rate was . percent in

Every village contains at least one precinct. Data from the Project of Precinctsallowed us to match precincts to villages. The electoral data were available at:http://electionresults.comelec.gov.ph/res_reg.html

the control group and . percent in the treatment group. The difference is not significant(p-value = .). Moreover, if the treatment did increase social desirability bias, this wouldhave made those who experienced vote buying more reticent to answer questions about it.The (insignificantly) higher non-response rate in the treatment group then constitutes a biasagainst the hypothesis that vote buying is higher among the treated respondents.

In cases where social desirability bias is present, a common solution has been to probe forvote buying indirectly, by asking respondents whether they were aware of any vote buying intheir village. This is a less reliable way to measure treatment effects, however. If the factof vote buying in the village is common knowledge, a change in the number of householdstargeted with vote buying by candidates need not affect at all the number of respondents whosay they are aware of vote buying. However, as a robustness check we also examine treatmenteffects on this variable.

Note that in some electoral contexts, it may be possible to ask voters not only aboutwhether their votes were bought, but also who bought them. In the area of the Philippineswhere we conducted the field experiment, however, PPCRV advised us that the second questionis highly sensitive, even though the first is not. While it would be convenient to have beenable to show direct evidence that incumbent vote buying was higher in treatment villages, wemarshall numerous pieces of indirect evidence that yield only one plausible interpretation: theinformation shock increased vote buying by incumbents.

Political Knowledge One test of the intervention’s effectiveness is whether treated house-holds were more knowledgeable about candidate budget allocations than untreated households.For each of the ten sectors about which respondents received information, respondents wereasked to name the candidate with the highest proposed allocation. Following Kling et al.(), we create an index aggregating the various indicators of knowledge of the campaignpromises by taking the simple average of the demeaned indicators (divided by the controlgroup standard deviation). So if Kis is individual i’s knowledge about sector s promises (i.e.,whether they correctly identified the candidate who proposed to spend the largest share ofthe LDF on sector s), then the knowledge index is.

Ki =1

10

∑s

Kis − K̄sσs

where K̄s and σs are respectively the control group mean and control group standard deviation.

Salience Another test of effectiveness of the intervention is whether treated householdscared more about local development spending than untreated households. We therefore asked

As discussed in more details below, the treatment effects on vote buying are robust to changes in the waymissing values are coded.

Respondents were not constrained in their responses and were free to – incorrectly – indicate that onecandidate was going to spend a higher share of the budget across all ten sectors.

respondents about six possible influences on their decision to vote. One of these was whethercandidates spend the municipal budget on things that are important to the household. Theother five were the preferences of friends and family; gift or money from the candidates beforethe elections; the candidates’ ability to use political connections to get money and projectsfor the municipality; fear of reprisal from candidates; and the approachability or helpfulnessof candidates. They rated how important each of these was on a - scale, from “notimportant” to “very important”. Respondents took flashcards, each with a reason for voting,and laid it on a worksheet with the numbers - , to indicate the importance of that factor.

We use two salience variables. One is simply the raw response: do treated householdsassign a higher score to the municipal budget criterion than untreated households? However,the treatment could have increased scores on all voting influences. To adjust for this, weconstructed a second measure of salience that removes the average answers in the other fivecategories. This measure allows us to demonstrate that, relative to the importance theyattach to other influences, treated households place more importance on the municipal budgetcriterion than untreated households.

Results: Effects on Knowledge and Vote Buying

Two direct effects of the experiment are of particular interest: did the information treatmentin fact increase relevant knowledge regarding candidate spending preferences? And did itinfluence vote buying? The results in this section first verify that treated voters are indeedmore informed about candidates and more likely to regard municipal spending as electorallysalient. We then report results that the intervention increased vote buying.

. Did the Treatment Increase Knowledge?

The descriptive statistics reported in Table suggest that voters tend to be poorly informedabout candidates’ promises: voters in the control group make an average of seven mistakesover the ten sectors. The information treatment increased voter knowledge of those promises.

To show this, we estimate regressions of the form:

Yijk = αTj + vk + uijk ()

where Yijk is the knowledge index for individual i in village j in pair k, Tj is a dummy equal toone if the campaign was implemented in village j, vk is a pair-specific unobservable and uijkis the usual idiosyncratic error term. To account for the way the randomization was carried

Although the ordering of the six alternatives may have affected the response, the ordering was the sameacross treatment and control groups.

To ensure that the six possible influences were all salient to respondents, the lists were extensively field-tested by one of the authors ahead of a similar survey carried out in the nearby province of Isabela.

out, standard errors are clustered at the village level. We also test if results are robust to theinclusion of the two variables that are not balanced between treatment and control.

The treatment did increase knowledge: voters in treatment villages were more likely toknow which candidate promised to spend the largest share of the LDF on any given sector(Table ). The treatment had no effect on dimensions of political knowledge not includedin the flyers (Table A.).

We further explore whether the treatment affected the salience of local development spend-ing for vote decisions. We estimate equation () where Yijk captures how salient sectoralallocations are for the vote choice of individual i in village j in pair k.

The treatment also increased the electoral salience of municipal spending. Treated respon-dents were more likely to report that candidate spending of the municipal budget is importantwhen they decide which candidate to vote for. This is true for both salience measures.

The information treatment does not mention vote buying and so should have no effecton the electoral salience of vote buying. It does not. The point estimate is small (.,p-value equal to .) and about one-tenth of the point estimates on the salience of budgetaryallocations (Table ). The salience results are robust to specifications with alternative controls(see Panels B and C of Table A.).

. Information Effects on Vote Buying

Survey results indicated high levels of vote buying: percent of voters in the control groupindicated they were offered money for their votes. Vote buying tends to take place a few daysbefore the elections. Therefore, even though our intervention was rolled out shortly before theelections, candidates had sufficient time to adjust their campaigning strategies should theyhave chosen to do so. In fact, we can show that vote buying increased in the treatment villages,estimating equations of the form:

Yjk = αTj + vk + ujk ()

where Yjk is the prevalence of vote buying in village j in pair k during the May elections.

The set-up is equivalent to the one used for equation ().The results in Table indicate that vote buying intensified in treated villages. These

effects are robust across specifications with alternative controls, shown in Table A.. TheFurther results, with different control variables and fixed effects, are available in Panel A of Table A..

Supporting the strength of our randomization strategy and the balance between treated and control groups,the point estimates are essentially constant across the four different specifications, though the standard errorsfall with the addition of more fixed-effects and control variables. As is the case with a number of other outcomevariables, the fixed effects explain a large share of the variation in voter knowledge.

Recall that, as indicated in the PAP, we run those regressions at the village-level. We obtain similar resultsif we run those regressions at the individual-level instead (Table A.).

The specifications we examine in Table A. were anticipated in the PAP. However, the PAP also regis-tered the prediction that the information treatment would reduce vote buying, based on the argument that

information treatment had a large and significant effect on our main outcome measure, thepercentage of village respondents who said that they were offered money for their vote. It ledto a . percentage points increase in vote buying ( percent of the control group mean).

A potential concern is that slightly more treated respondents refused to answer the votebuying questions, . percent versus percent in the control group. We note above thatthis difference is both insignificant and creates a bias against the findings we report here.In addition, several checks indicate that differential rates of non-response cannot account forour results. In the results reported in Table non-responses are coded as missing. To checkrobustness, we first recoded all non-responses as "yes", someone in fact offered the respondentmoney for her vote, to reflect the possibility that non-response reflects reluctance to reportvote buying that actually occurred. The top panel in Table A. shows that treatment effectsremain large and significant. In the bottom panel of Table A., we instead code ’refuseto answer’ as "no", to verify robustness to the less plausible assumption that more reticentrespondents were actually not offered money for their votes. Although the treatment effectdrops from . percentage points to . percentage points, it remains significant controllingfor pair fixed-effects, as in Table . We obtain similar results - with higher levels of statisticalsignificance - when we run those regressions at the individual-level (Table A.).

Finally, Lee (), proposes that confidence intervals be adjusted to take non-responseinto account. We derive the Lee bounds, . and ., which allow us to reject the nullhypothesis that the treatment increased vote buying by less than . percentage points, con-sistent with the more heuristic approach to recoding non-responses.

For completeness, we also report the treatment effect on the share of respondents whowere aware of instances of vote buying in their village. By construction, this variable is lesssensitive to the treatment, since it should remain stable, no matter how many households areoffered money for their votes, as long as the presence of any vote buying at all in the villageis common knowledge. Nevertheless, the treatment effect is nearly the same, . percentagepoints. It is not significant in the village level regressions (Table ). However, in individuallevel regressions, reported in Panel A of Table A., the treatment effects are highly significantand of almost identical magnitudes to the ones obtained with our preferred measure of vote-buying incidence.

Qualitative evidence from local observers in the study area confirms these results: votebuying occurs in the days before the election and candidates and their brokers can re-targetvote buying quickly. In many cases, the candidates contacted PPCRV with specific questionsabout the intervention activities. These sources also reported that candidates redoubled effortsto buy votes in the treatment villages and that most of the additional vote buying occurred

subsidizing promises would lead candidates to substitute away from vote buying in treated areas as in Keeferand Vlaicu (). We did not anticipate widespread voter ignorance of the Local Development Fund andthe fact that, in the face of this ignorance, our treatment would lead households to substantially revise theirevaluations of incumbent performance. Note that, while the intervention increased vote buying, we argue thatthis was a result of an intervention that actually increased incumbent incentives to improve voter welfare.

on election day or the day before.

Candidates might have financed the additional vote buying in treatment villages by in-jecting additional resources into their campaign, raising the welfare of vote buying recipientswithout reducing the welfare of other voters. Candidates might have instead transferred re-sources from villages that did not receive the flyer to those that did. The model predictsthat they would have pursued the first option, but we do not have sufficient information todiscriminate between these two cases.

. Treatment Effects are Largest When Respondents Report Fewer PublicWorks

The field experiment also supports the mechanism through which the information shock shouldhave increased vote buying: the vote buying effects of the flyer were strongest among thoserespondents who reported fewer recent projects in their villages. Respondents who receivedthe flyers and who reported fewer projects were more likely to report vote buying in the fieldexperiment, just as in the survey experiment they were less likely to express support for theincumbent.

The endline survey of the field experiment asked voters to report public investments intheir village that had been financed by the incumbent mayor since the previous election.

We therefore add an interaction term, public investment financed by the mayor and treatmentstatus, to the earlier vote buying regression. We expect that the positive treatment effect onvote buying should be lower in villages that reported more public investment. Consistent withthis, the interaction of treatment and reported public investment in Column of Table issignificant and negative.

We also can ask whether the effects of the information intervention on vote buying differdepending on whether villages report greater than or less than median public investment bythe incumbent as the relationship might not be linear. In villages reporting below-medianpublic investment, the treatment significantly increased vote buying by . percentage points(Column of Table ). The treatment effect in villages with above median public investmentwas tiny and insignificant.

Interviews conducted during the debriefing with PPCRV staff after the May elections, with follow-upinterviews conducted in April .

It is not plausible that respondents who report more public investment had received that investmentbecause they had more demanding performance thresholds. On the one hand, incumbents should prefer tosatisfy lower performance thresholds before they satisfy higher thresholds. Knowing this, voters should not sethigher thresholds. On the other hand, if voters who reported lower public investment had lower thresholds,incumbents would have had no reason to increase vote buying in their villages, contrary to what we observe.

Those results are robust to controlling for the number of registered voters in the village, average yearsof educations of household heads in the village, the share of households who benefit from the government’slarge-scale CCT programme, the share of households engaging in farming, the share of households with at leastone group member and the share of households who participate in bayanihan activities, and their interactionswith the treatment dummy (Table A.). This reduces concerns that the interaction with number of projectsis actually capturing an interaction with other village-level characteristics. These results offer an information

One might worry that self-reported public investment is influenced by the treatment. Infact, though, respondents in treatment and control villages report similar rates of municipalprojects: . on average in the control group and . in the treatment group. We are unableto reject the null that the means are equal (p-value = .). Those results are available inTable A..

. Vote Buying Offset Treated Voters’ Disappointment with Incumbents

A second piece of indirect evidence for increased incumbent vote buying emerges from treat-ment effects on support for the incumbent. The survey experiment indicates significantlylower support for the incumbent among respondents who are informed about the Local Devel-opment Fund. Treated voters in the field experiment, however, were no less likely to supportthe incumbent than untreated voters, consistent with incumbents having responded to thetreatment with greater vote buying. Rows and of Table report precisely this result.Consistent with incumbents using vote buying to offset the disappointment of treated voters,support for the incumbent among treated voters should be no different than among controlvoters. Incumbent vote share, whether official or self-reported, was no different in treatedor control villages.

Although vote buying is significantly greater in the treated villages, both self-reportedand official incumbent vote shares are indistinguishable in treated and control villages. Thereare only three possible explanations for this. One is that the treatment had no effect onsupport for either incumbent or challenger, but instead simply caused both to campaign moreintensively, leading to greater vote buying by both sides in treatment villages. The second isthat the treatment had a positive effect on support for the incumbent, offset by challenger votebuying. The third is that the treatment had a negative effect on support for the incumbent,offset by incumbent vote buying. Results from the survey experiment are only consistent withthe third interpretation. Three further arguments support this conclusion.

First, treatment effects are strongest where the incumbent provided the fewest publicgoods, not where the incumbent provided the most. Consistent with the survey experimentresults showing a reduction in incumbent support, this rejects the competing hypotheses thatthe treatment had either no effect on voter preferences, or had a positive effect on preferencesfor the incumbent.

Second, vote buying is a demanding strategy and incumbents confront different costs ofengaging in it. Those with lower vote buying costs should increase vote buying as a result ofthe experiment, offsetting the loss of support induced by the treatment. High cost incumbents,in contrast, should react less and experience lower levels of support as a consequence. The

rationale for the negative correlation that Khemani () documents between public good provision andvote buying in the Philippines. For completeness, we report the heterogenous treatment effects for the otheroutcomes as well (Table A.).

Full results are reported in Table A..

data are consistent with this predicted pattern. For each municipality, we compute the levelsof vote buying in the control group and distinguish municipalities where control group votebuying is lower and higher than the mean. Levels of control group vote buying vary greatlybetween the two municipalities: . percent in the former and . in the latter. We argue thatincumbents in the former were more constrained in their ability to respond to the treatment.

In Column of Table we show that the treatment increased vote buying by . percent-age-points in municipalities with high levels of vote buying in the control group. The pointestimate in the other municipalities is minuscule (. percentage-points). Conversely, in Col-umn of Table we show that the treatment decreased support for the incumbent by .percentage-points in municipalities with low levels of control group vote-buying. Strikingly,this effect is of similar magnitude as the one obtained in the survey experiment. The pointestimate in the other municipalities is tiny (. percentage-points). Those results are robustto controlling for the number of projects financed by the incumbent between and (Columns and of Table ).

This pattern is consistent with incumbent vote buying to offset disappointment. It isinconsistent with the possibility that the treatment increased support for the incumbent. Ifthe treatment had increased incumbent support, then in municipalities with low levels of votebuying (in the control group), treated respondents should have expressed greater support forthe incumbent than control respondents. Instead, they express less.

The pattern is also inconsistent with the possibility that the treatment increased campaignintensity and had no partisan effects. In this case, voters in municipalities where incumbentsdid not respond to the treatment by buying more votes should have been no more likely tosupport a candidate in the treated than the control group. Instead, treated voters were farless likely to express support for the incumbent.

Third, qualitative evidence also supports our claim that incumbents were responsible fortreatment-induced vote buying. Two local PPCRV affiliates in Ilocos Sur confirmed thatincumbents conducted additional vote buying in the treatment areas after our interventionwas completed. They specified that most of the additional vote buying occurred on electionday or the day before.

Related results indicate that among respondents whose votes were not bought, treated respondents weresignificantly (. percentage points) less likely to support the incumbent than control respondents (TableA.). This difference is robust to adding a number of controls in addition to the pair fixed effects. The modelwe present earlier predicts that incumbents react to the information shock only by changing vote buyingamong the treated group. The information shock does not change equilibrium incumbent vote buying amongunaffected voters. The difference in support among respondents whose votes were not bought indicates thatthey confronted logistical and financial constraints that prevented them from buying as many additional votesin the treated group as they might have wanted.

Interviews conducted during the debriefing with PPCRV staff after the May elections, with follow-upinterviews conducted in April .

. Candidate Policy Intentions and Respondent Preferences over Candi-dates

Observers of Philippines elections, especially municipal elections, agree that programmaticpromises, such as those related to the allocation of the LDF, are not salient. Indeed, if theywere important, candidates should have already disseminated their intentions regarding theLDF prior to our intervention. They did not. In this section, we present both theoretical andempirical arguments that the promises embedded in the information treatment did not affectvoter behavior in the elections.

In theory, if candidate LDF allocation intentions had affected voter attitudes, vote buyingshould have dropped in treated areas; instead it rose. For example, Cox () examinesthe expansion of the franchise in Great Britain and shows that it increased the salience of(credible) party programs and reduced vote buying. Keefer and Vlaicu () show thata decline in the probability that a party will renege on its pre-electoral promises reducespoliticians’ payoffs to vote buying.

We can also demonstrate empirically that information about candidates’ allocation inten-tions had no effect. For those intentions to have mattered, it must have been the case thattreated respondents with preferences closest to one candidate’s intended allocations shouldhave been more likely to have preferred that candidate compared to control respondents. Inaddition, the closer are a voter’s preferences to the policy announcements of one candidaterelative to the other, the more difficult it is to sway that voter with vote buying. Hence,reported vote buying should also fall the greater is respondent alignment with one candidatecompared to the other.

To investigate these issues, we collected data on respondents’ candidate preferences andvote choice. Respondents rated all mayoral candidates on a - scale (strongly disagree tostrongly agree) and were also asked directly whom they voted for. In order to reduce thetendency of respondents to claim they voted for the winner when they did not, we used asecret ballot.

We also asked respondents to express their preferences over the same ten spending cat-egories that were given to the mayoral candidates. Like the candidates, respondents weregiven tokens and asked to allocate the tokens in any manner they wished across the tencategories. We then calculated how close the preferences of the candidates were to those ofthe household by comparing the share S that voter v allocated to sector s with the share thatcandidate c allocated to the sector. The total spending over which the candidate and voter

See also Cox and Kousser ().Respondents were given ballots with ID codes corresponding to their survey instrument. The ballots

contained the names and parties of the mayoral candidates in the municipality, in the same order and spellingas they appeared on the actual ballot. The respondents were instructed to select the candidate that they votedfor, place the ballot in the envelope, and seal the envelope. Enumerators could not see the contents of theseenvelopes at any point and respondents were told that the envelopes remained sealed until they were broughtto the survey firm to be encoded with the rest of the survey.

agree is given by an agreement index, defined as Avc =∑

smin (Svs, Scs).Table A. reports results of a vote choice regression where we control for both the treat-

ment, the alignment between the voter’s preferences and the candidate promises and theirinteractions. If the results were driven by promises, treatment group voters should expressedsupport for the candidate whose promises were more closely aligned with their own preferences.This alignment should have no effect on control voters, who are unaware of the promises. Werun those regressions with both candidate preferences and vote choice. In both cases the pointestimates on the interaction term is very close to zero and not significant.

Further if policy stances matter, then the relative distance between candidate’s policystances and the policy preferences of respondents should affect key outcomes, such as knowl-edge and vote buying, and those effects should be greater among treated households. TableA. shows, in contrast, that the relative policy stances almost never matter. Those for whomone of the candidate’s promises are relatively closer to the respondent’s preferences do notreport differences in vote buying nor in the salience of spending. In all these cases, the treat-ment effect (higher vote buying and greater salience of municipal spending) is unaffected byrelative policy stances.

A potential concern with the policy preferences variable is that it represents a choice thatrespondents are not used to making. However, respondent preferences seemed to correspond totheir family circumstances. We regress preferences on a number of household characteristicsthat should be correlated with preferences for a given sector. For example, families withchildren should favor spending on education and farmers should favor spending in agriculture.Results presented in Table A. suggest that stated preferences over spending priorities matchobservable household characteristics.

Allocation preferences were collected after the information about candidates’ promises hadbeen distributed to voters in the treatment group. It is therefore possible that respondentsmight have adjusted their preferences to match their preferred candidate’s promises. Twopieces of evidence suggest that this is not the case. First, we are unable to reject the nullhypothesis that the alignment between respondents and their preferred candidate is the samebetween the treatment and control group. This holds whether we define the preferred can-didate as the top-ranked candidate on the - scale or as the candidate whom respondentsindicated voting for in the secret ballot exercise. Second, the correlation between alignmentand support for given candidates is essentially the same across the treatment and controlgroups (Results in Table A.).

We obtain similar results when we run those regressions at the precinct (for turnout) and precinct-candidate(for candidate vote share) levels (Table A.).

. Comparisons of Candidates and Assessments of Candidate Quality

Last, we show that potential alternative explanations regarding voter perceptions of candidatequality are unlikely to be driving the results. One possibility is that the treatment raised theprofile of the challenger relative to that of the incumbent, making the mayoral race morecompetitive and driving both candidates to increase vote buying. Another possibility is thatthe treatment affected voter beliefs about candidate quality, prompting candidates to respondwith vote buying.

These potential explanations are inconsistent with the results in three ways. First, thesurvey experiment demonstrated a measurable reduction in incumbent support even withoutreference to either candidate, suggesting that voter disappointment with the incumbent doesnot depend on comparison with the challenger. Second, the flyer had no information thatvoters could use to assess candidate quality, other than the fact that both candidates werecapable of formulating a policy regarding the allocation of the Local Development Fund.Third, the survey asked respondents for their opinions on four candidate qualities, honesty,approachability, experience and political connectedness. We observe no treatment effects onany of them. Results are summarized in Table A..

Conclusion

We show that even in clientelistic settings, voters use information rationally, making informa-tion campaigns a potentially powerful and cost-effective way to decrease information asym-metries between voters and politicians. Even providing ostensibly neutral information aboutgovernment capabilities allows voters to make their own assessment about candidate perfor-mance.

We combine a theoretical model with two experiments to test the effects of informationabout the existence of a spending program in an environment where candidates cannot makecredible commitments. In the model, information shocks that raise voters’ thresholds forincumbent performance shortly before an election oblige incumbents to do more to increasevoter welfare than they anticipated. With little time before the election to improve theprovision of public goods, incumbents turned to vote buying.

The survey experiment provides direct evidence that merely informing individuals of theexistence of the spending program reduces support for incumbents; especially those who haveunder-provided public goods during their term in office. We further explore these effects in thecontext of real world elections using a unique field experiment providing voters with the same

The exact question in the survey is: “Now we are going to show you a set of worksheets, one for eachcandidate, as well as some flashcards containing some traits [Approachable/Friendly; Experienced in politics;Honest; and Politically well-connected] that candidates might have. For each of these traits, please place themon the worksheet of the candidate that you most associate with that trait. You may place the same trait onboth worksheets or you may choose not to place a trait at all if you feel that it does not apply to any of thecandidates."

information just prior to the May municipal elections in the Philippines. Consistentwith the survey experiment results, the intervention led to a decrease in voter support forincumbents, prompting the subsequent incumbent response, which in this case took the formof increased vote buying. The intervention led to significant changes in voter knowledge aboutincumbents and vote buying.

The findings have implications for improving the accountability effects of elections in de-veloping countries. They demonstrate that voters are poorly informed about what politicianscan do for them and that relatively simple information interventions have a significant ef-fect on this information asymmetry. Moreover, since the asymmetry reduces the incentivesof incumbents to improve citizen welfare, such an intervention has