Do Government Audits Reduce Corruption? Estimating the Long-Term Impacts of Exposing Corrupt Politicians

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1 Do Government Audits Reduce Corruption? Estimating the Long-Term Impacts of Exposing Corrupt Politicians Eric Avis UC Berkeley Claudio Ferraz PUC-Rio October 2015 Frederico Finan UC Berkeley Abstract This paper examines whether Brazil s anti-corruption program, which audits municipalities for their use of federal funds, reduces corruption among local governments. To estimate this effect, we exploit the fact that some municipalities are audited multiple times and at random. We find that being audited in the past reduces future corruption by 7 percent. We interpret these reduced-form findings in the context of a political agency model, which we proceed to structurally estimate. Based on our estimated model, we then decompose the effects of the audits along three potential channels: 1) a political selection effect, 2) an electoral disciplining effect, and 3) a non-electoral disciplining effect. We find that the audits increased the perceived threat of the non-electoral costs of engaging in corruption, and that this channel accounts for 2/3 rd of the reduction in corruption. The disciplining effect coming from elections explains the remaining reduction in corruption. We find no evidence of a political selection effect. Keywords: Corruption, Audits, Political Selection, Political Accountability JEL:. We are grateful to Department of Economics, Evans Hall, Berkeley, California eavis@econ.berkeley.edu Department of Economics, Pontifícia Universidade Católica do Rio de Janeiro (PUC-Rio), Rua Marquês de São Vicente, 225- Gávea Rio de Janeiro, RJ, , Brasil. cferraz@econ.puc-rio.br; and BREAD Department of Economics, Evans Hall, Berkeley, California ffinan@econ.berkeley.edu; and BREAD, IZA, NBER

2 1 Introduction Countries throughout the world are increasingly adopting anti-corruption measures in response to the widely held belief that corruption is an important cause of underdevelopment. A central component of many of these anti-corruption strategies is the use of audits. The expectation being that when accompanied with appropriate punishment, enhanced monitoring can discipline individuals from engaging in malfeasance (Becker and Stigler (1974)). With politicians however, the predictions become less clear. Although the threat of an audit can discipline politicians in the short run, it can also make it harder for voters to screen out bad politicians, thus increasing corruption in the longer run (Besley (2007)). The question of whether audits are an effective policy for reducing political corruption is an empirical question that the existing literature has yet to shed much light upon. There are several challenges to identifying the effects of an audit on corruption. Audits are not often conducted at random, but are instead targeted towards specific groups or individuals. In this case, it is hard to determine whether any differences in subsequent corruption levels are due to the audits or to underlying (unobservable) differences in the propensity to engage in corruption. Even when the audit is conducted at random, we do not typically observe corruption levels in places that were not previously audited. In this paper, we overcome these obstacles to examine the effects of federal audits on corruption in local governments. We do so in the context of Brazil s anti-corruption program, which not only audits municipal governments at random, but also provides objective measurements on a municipality s misuse of federal funds. The program has also been in existence since 2003 and has audited 2,241 municipalities, many of which multiple times. As a result, for several rounds of later audits, we are able to compare the corruption levels discovered among the municipalities that are being audited for the first time (control group) to the corruption levels of municipalities that had been audited in the past (treatment group). Because municipalities are selected at random, this simple comparison estimates the causal effects of being audited on future corruption levels. Corruption levels are significantly lower among treated municipalities compared to control municipalities. Based on our preferred specification, the audits reduced total acts of corruption by 7.1 percent. The average municipality in our sample receives R$15,000,000 in federal transfers per year. Based on our estimates of a random sample of audit reports, 30 percent of the funds audited were found to be diverted, implying that the audits reduced corruption by R$320,000 per year per municipality. One advantage of our data is the ability to distinguish between active and passive 1

3 waste (Bandiera et al. (2009)). We do not find any evidence that the audits reduced passive waste. We also examine the distribution of impacts on each level of corruption. We find some evidence that the audits were more effective in high corruption places relative to low corruption places. The treatment effects do not however, vary significantly based on local characteristics, such as access to local media, education levels, and income per capita. We interpret the main findings in the context of a simple model of political accountability, whereby politicians are heterogeneous in the propensity to engage in corruption and voters do not observe their actions. Based on this framework, there are several reasons why the audits may have led to a reduction in local corruption. First, the audits may have reduced corruption through a political selection effect. As documented in Ferraz and Finan (2008), in places that were audited before the election, voters were able to reward good and punish bad incumbents who were up for re-election. Second, the audits may lead to a stronger discipline effect. If an audit increases a mayor s subjective probability of being detected and he has re-election concerns, then he has less incentive to engage in corruption. However, even if a mayor does not care about re-election, an unfavorable audit can comes with other costs, such as the possibility of prosecution or reputational costs. Thus, an audit can discipline politicians along this margin as well, which we have termed as a reputation effect. Finally, the audits may also affect the political environment more generally by inducing a better selection of candidates (i.e. an entry effect), or spurring more grass-roots monitoring. In the reduced-form, we find that strong evidence in support of a reputation effect. Compared to non-audited municipalities, corruptions levels are 13.5 percent lower in municipalities where the mayor experienced (by chance) multiple audits within the same term. Moreover, when we compare how these effects vary across mayors with and without re-election incentives, we find that the effects are present even among those who are no longer eligible for re-election. Meanwhile, the evidence for the other channels is much weaker. For example, we find that audits significantly reduced corruption even among new mayors where the audits occurred in the previous term. Although this results is consistent with a potential entry effect, it can also represent a reputation and discipline effect. When we net out these other effects, we find no evidence of an entry effect. Additionally, we find little evidence that the audits affected the types of candidates that run for office. We also do not find much support for a political selection effect. Although mayors who were audited before the election and subsequently re-elected engage less corruption compared to non-audited places, this difference (in addition to a political selection effect) captures both a reputation effect and the selection effect induced in absence of an audit. Once we account for these other effects, we find that the audit effects resulting from political selection appear to be 2

4 minimal. An important limitation of these reduced-form comparisons is that they do not allow us to capture the full impact of political selection, or disentangle a potential entry effect. As a result, we bring our model to the data to separate out these various channels and quantify their relative magnitudes, which is important because they carry different policy implications. To this end, we then uses our estimates of the primitives of the model to conduct alternative policy simulations aimed at further reducing corruption. Our structural estimates provide several additional insights. We find that mayors assign a 18 percent probability of being detected of corruption in places that have been audited in the past compared to only 4 percent in places that have not. In equilibrium, this leads to 14.6 percent of corrupt mayors pretending to be non-corrupt in the audited municipalities compared to only 3 percent in the nonaudited municipalities. Based on these estimates, 33 percent of the difference in corruption levels between audited and non-audited municipalities can be attributed to a discipline effect. Consistent with our reduced-form findings, the remaining difference is not due to a selection effect, which only accounts for 1 percent of the difference, but rather a reputation effect. Based on these findings, we consider two types of counterfactual policies. First, we simulate an increase in the probability that voters observe the rents extracted by the incumbent. This would be the case if the program increased the frequency of audit lotteries or the number of municipalities audited in each lottery. Second we simulate an increase in the share of non-corrupt mayors in the pool of candidates. Based on these simulations, we find that a 20 percent increase in the probability of that corruption is detected leads to a 15 percent reduction in corruption. However, if one could simply increase the proportion of non-corrupt mayors in the candidate pool by 10 percent, the corruption would fall by 30 percent. Our findings are related to three broad literatures. Our study contributes to a large literature on the determinants of corruption and the design of policy aimed at curbing corruption. 1 Within this literature, our study is most closely related to three studies in particular. Bobonis et al. (2011) find that the audit reports released just prior to the election (compared to those released after an election) induced a significant short-term reduction in municipal corruption levels, but this difference disappears in the subsequent rounds of audits. An important distinction between our studies is that in our context the audits are conducted at random, and thus politicians are not able to anticipate them. Olken (2007) conducted a randomized experiment on auditing. Prior to start of a national wide infrastructure project, villages in Indonesia were randomly assigned into groups with differ- 1 See Olken and Pande (2012) for an extensive review of the current literature. 3

5 ent audit probabilities. The treatment villages were told that they would audited with a 100 percent probability, whereas the control villages only had a 4 percent probability of being audited. Based on an independent assessment of costs, the study found that 24 percent of reported funds were found to be missing, but when faced with a certain audit this difference was reduced by 8 percentage points. Zamboni and Litschig (2015) investigate the effects of a randomized experiment conducted by the CGU designed to to test whether increased audit risk reduces corruption and mismanagement. In this experiment, the CGU announced in May of 2009 to 120 municipalities that in one year time, 30 of them would be randomly selected for audit. During that lottery an additional 30 municipalities were also selected as part of the regular auditing process. Based on this temporary increase in audit risk of about 20 percentage points, the authors found that the treatment reduced the proportion of local procurement processes involving waste or corruption by about 20 percent. Our study complements these studies by demonstrating how even when audit probabilities are the same across regions, audits can still reduce corruption by affecting an incumbent s subjective probability of being detected. Our findings also related to studies that try to distinguish between active and passive waste. Bandiera et al. (2009) is a primary example. Using data on public procurement from Italy, they find that more than 80 percent of waste can be classified as passive. In contrast, only 26 percent of the irregularities discovered in the audit reports are classified as passive waste. However, similar to Bandiera et al. (2009) we do not find any evidence that active and passive waste are positively correlated. Our study relates to growing empirical literature that examines the relationship between electoral accountability and politician performance. 2 Exploiting variation in term limits, a series of papers have shown robust evidence that incumbents respond to re-election incentives. For example, Besley and Case (1995) show that re-election incentives affect the fiscal policy of U.S. governors, while List and Sturm (2006) provide evidence that term limits even influence secondary policies, such as environmental policy. In relation to the Brazilian context, Ferraz and Finan (2011) find that mayors who are in their second term, and hence do not have opportunity for re-election, engage in much more corruption relative to mayors with re-election incentives. Similarly, de Janvry et al. (2012) find that Brazil s Bolsa Escola a conditional cash transfer program that was targeted in a decentralized manner performed much better in places where mayors had re-election incentives. While these studies provide convincing evidence consistent with standard political agency models, they are unable to quantify the electoral selection effects that are also central to models of political accountability. Our paper thus complements this body of evidence by demonstrating how with 2 See Ashworth (2012) for an excellent review of this literature. 4

6 some additional structure, we can disentangle selection effects from incentives effect, and quantify their relative impacts on rent extraction. In this respect, our study is similar to Aruoba et al. (2015), who also estimate a model of political accountability to quantify the discipline and selection of U.S. gubernatorial elections. Using data from of U.S. governors, they find that the possibility of re-election leads to 13 percentage point increase in the fraction of governors who exert high effort in their first term in office, as measured by voters job approval. Also set in a different, they too find weaker selection effects: the fraction of good governors rises by 8 percentage points from the first to second term in office. In a related study, Alt et al. (2011) also use gubernatorial elections data from the U.S. to disentangle the discipline and selection effects of elections. By comparing states with different term limit laws, they find discipline and selection effects of similar magnitudes, with using as outcomes per capita spending and taxes. Finally, our study also contributes to a literature in public finance that explores the effects of being audited in the past on future tax compliance. Kleven et al. (2011) conduct a field experiment on tax enforcement in Denmark, in which tax filers were randomly selected to be audited. In the following year, a threat-of-audit letters were sent to both groups. As in our study, they find that prior audits have a significant effect (and even large effect that the threat of an audit) on self-reported income. The rest of the paper is organized as follows. Section 2 provides background on the Brazil s anticorruption program and presents the data used in the empirical analysis. Section 3 presents the theoretical framework. Section 4 discusses our research design and in Section 5 we present our reduced-form findings. In Section 6 we discuss the estimation of the model and present our counterfactual simulations. Section 7 concludes. 2 Background and Data 2.1 Brazil s Anti-Corruption Program In April 2003 Brazil s Controladoria Geral da União (Office of Comptroller-General) launched an anti-corruption program targeted at municipal governments. It consisted of random audits of municipalities for their use of federal government funds. The program, named Programa de Fiscalização por Soteios Públicos, started with the audit of 26 randomly selected municipalities across different states in 2003 and then moved towards auditing 50 and later 60 municipalities every two to three months. The lotteries are publicly held in conjunction with the national lottery in Brasilia and all municipalities with a population of up to 500,000 inhabitants are eligible for selection. 5

7 Once a municipality is chosen, the CGU gathers information on all federal funds transferred to the municipal government during the previous three to four years and issues inspection orders. Each one of these orders stipulates an audit task for a specific government project (e.g. school construction, purchase of medicine, etc.). 3 Once these inspection orders are determined, 10 to 15 auditors are sent to the municipality for one to two weeks to examine accounts and documents, to inspect for the existence and quality of public work construction, and the delivery of public services. These auditors are hired based on a competitive public examination and earn highly competitive salaries, thus the incentives for corruption are lower than other bureaucrats in the federal level administration. Moreover, the inspections are usually done by a team which reduces the opportunity for corruption among individual auditors. 4 After the inspections are completed, a detailed report describing all the irregularities found is submitted to the central CGU office in Brasilia. The central unit unifies the information and publishes a report in the internet. These reports are also sent to the Tribunal de Contas da União (TCU), to public prosecutors, and to the municipal legislative branch. Over time the program has changed in order to improve the auditing capabilities of the CGU. Because it is easier to audit several government programs and contracts in smaller municipalities, the CGU decided in August 2005 to target the audits in larger municipalities those above 20,000 inhabitants to a limited number of sectors, which are also selected at random across lotteries. In the 17 th lottery that took place in August 2005, for example, the sectors chosen were social assistance, crime prevention, and industrial policies. Municipalities smaller than 20,000 inhabitants, on the other hand, were subject to audits in all sectors (e.g education, health, agriculture). In May 2007 the CGU further split larger municipalities into two groups: those between 20,000 and 100,000 inhabitants and those with more than 100,000 people. While those localities with less than 20,000 inhabitants could be audited in any sector, municipalities with 20,000 to 100,000 inhabitants were audited in transfers made by the ministries of education, health, social assistance, crime prevention, and industrial policy. Those localities with more than 100,000 inhabitants were audited in resources transferred for education, crime prevention, and industrial policy. Finally in August 2011 the CGU changed the target of the audits for a third time. Starting with the 34 th they increased the thresholds from 20,000 to 50,000 and made the second threshold vary from 50,000 to 500,000. Although these changes affect the areas in which municipalities can be audited, they don t affect 3 Auditors do not have discretion in auditing other projects. In case they find clear evidence of corruption in their field work, they need to notify the central unit of the CGU who will then decide whether to issue a new inspection order. 4 In Ferraz and Finan (2008), we find no evidence that auditors manipulate the audit reports. 6

8 the probability that localities are audited. The lotteries are done by state so the probability that a municipality gets audited is constant for municipalities within the same state. The number of municipalities that get audited within state has varied both across time and across states. For smaller states such as Alagoas only 1 or 2 municipalities are typically drawn in a single lottery, whereas for a large state like Minas Gerais, with over 853 municipalities, as many as 8 municipalities have been drawn in a single lottery. Overall, as we see from Table 1, the implied audit probabilities are quite small, with the average being only 1.3 percent (s.d.= 0.005). Once a municipality is audited, it can only be audited again after 2 lotteries have elapsed. As of February 2015, there have been 2,241 municipalities audited across 40 lotteries, and over R$22 billion dollars worth of federal funds investigated. By various accounts, the program has been considered a major success. The information obtained in the audits has led to several largescale crackdowns and the arrests of hundreds of politicians, bureaucrats, and firms involved in the diversion of public resources. Local legislatures and the electoral commission have also used the reports to impeach and prohibit corrupt mayors from running for office. Moreover, as? have shown, the information available from the audits have been widely used in political campaigns and have affected the selection of politicians at municipal elections. Despite these events, there is no quantitative evidence on whether the audits have effectively reduced corruption in Brazilian municipalities. 2.2 Data We use the coding of the audit reports provided by the CGU auditors to measure corruption and mismanagement of resources at the local level. While all of the audit reports are posted online, starting with the 20 th lottery in March 2006, the CGU began to code the information contained in the reports for internal use. For each inspection order, the dataset contains information on the sector and government program, the amount transferred to the municipality, and a list of findings. For each finding, the auditors describe the irregularity found and assign a code that classify irregularities into three categories of wrongdoing, ranging from simple procedural issues, such as missing documents on a procurement process to moderate and severe irregularities, such as large withdrawals from checking accounts with no receipts on how the resources were spent. To illustrate the classification scheme used by the CGU, take for example the municipality of Chaval in Ceará, which was audited in the 20 th lottery. The auditors went to the municipality with 25 auditing orders. While auditing a program that finances school buses for students attending primary 7

9 schooling, they discovered two irregularities. For the first irregularity, which was classified as moderate, a representative of the mayor used a check to withdrawn R$1,200 without proving how the money was spent. The second irregularity, which was classified as severe, took place during the procurement of transportation services. The contract was awarded to a firm that did not match the original proposal, and the value of the contract was for a different amount than what was offered. Based on this information from CGU, we construct a measure of passive and active waste. Our measure of active waste (i.e. acts of corruption) is the number of irregularities by lottery and municipality that were classified as either moderate or severe by the CGU. For our measure of passive waste (i.e. acts of mismanagement), is the number the irregularities by lottery and municipality that were associated with administrative and procedural issues. In Figure 1, we plot the distributions of irregularities associated with active and passive waste per service order. The audits discover on average 2.5 acts of corruption and 0.88 acts of mismanagement per service order, suggesting that 73.6 percent of the irregularities found during an average audit involves some acts of corruption. To these figures in perspective, Bandiera et al. (2009) estimate only 20 percent of waste found in Italy s public procurement process was due to corruption. Similarly, Olken (2007) argues that the main reason why villages that audited in Indonesia did not significantly reduce their corruption is because the audits mostly reveal acts of mismanagement as opposed to acts of malfeasance. Similar to Bandiera et al. (2009) we do not find any evidence that active and passive waste are positively correlated (correlation coefficient = 0.02). In Figure 2, we plot the average number of irregularities associated with active and passive waste by lottery. While our measure of active waste has been increasing steadily over time, the acts of passive waste has been much more variable, particularly in recent audits. Given the changes to the auditing protocol over time, one should be cautious to overinterpret this temporal variation. Three other data sources are used in this paper. The political outcome variables and mayor characteristics come from the Tribunal Superior Eleitoral (TSE), which provides results for the municipal elections. These data contain vote totals for each candidate by municipality, along with various individual characteristics, such as the candidate s gender, education, occupation, and party affiliation. With this information, we matched individuals across elections to construct measures of reelection and whether mayors are serving on a first versus second-term. Data on municipal characteristics come from the Brazilian Institute of Geography and Statistics (Instituto Brasileiro de Geografia e Estatística (IBGE)). The 2000 population census provides several socioeconomic and demographic characteristics used as controls in our regressions. Some of these key variables include per capita income, income inequality, population density, share of the popu- 8

10 lation that lives in urban areas, and share of the population that is literate. To control for different institutional features of the municipality, we also use information from 1999 municipality survey, Perfil dos Municípios Brasileiros: Gestão Pública. This municipal survey characterizes not only various aspects of the public administration, such as budgetary and planning procedures, but also more structural features such as the percentage of roads that are paved, whether the municipality has a judge, among others. Moreover, the survey provides our key measures of the availability of media, namely the number of radio stations and the number of daily newspapers. The richness of this dataset allows us to comprehensively check the validity of our research design, and control for any potential confounding factors in the regressions that do not entirely rely on the randomization. Table 2 presents summary statistics for the municipalities in our sample, by whether they were audited previously or not. For each characteristic, we also present the difference between these characteristics. As expected from the random assignment, there is little difference between places that were audited for a first time compared to those that have previously been audited. Out of 15 characteristics, only one is statistically significant at the 10 percent level. We also fail to reject the hypothesis that all the variables are jointly significant (F-test=1.17; p-value=0.30). Overall the results from Table 2 suggest that the lottery used by the CGU was effective. 3 Model We consider the following two-period model of political accountability. 5 In the first period, an incumbent politician chooses whether to extract high or low rents. The voter then observes a noisy signal of the rents, and chooses whether to reelect the incumbent or select a challenger who is randomly drawn from the pool of potential politicians. In the second period, the incumbent decides whether to extract high or low rents, and the game ends. The incumbent s problem During a term, the incumbent chooses whether to extract low rents" or high rents", i.e. an action from the set{l,h}. She obtains a rent µ L if she picks low rents and µ H if she picks high rents. We assume that her utility is linear in rents. 5 We also solve the infinite-period model, which is presented in Appendix B. We present and solve the two-period model because it yields qualitatively the same predictions as the more general infinite-period model. 9

11 There are two types of politicians, congruent politicians and dissonant politicians. Congruent politicians set policy to maximize the voter s objectives, whereas dissonant politicians seek to maximize private gains. Thus, congruent politicians always choose to extract low rents. Dissonant politicians choose between extracting high rents and low rents by comparing the immediate benefits of higher rents to the cost of a smaller reelection probability. At the start of each incumbent s first term, the incumbent privately observes her cost of extracting high rents, γ. We assume that γ is drawn from a distribution F γ with support on [0, µ H µ L ], so that extracting high rents always yields a higher private benefit than extracting low rents. The cost to extract low rents is normalized to 0. The cost of rent extraction may be interpreted in a number of ways. It may reflect the incumbent s competence, the importance of special interests, or a social preference for the voter. In her second term, a dissonant incumbent will always choose to extract high rents because γ µ H µ L. In her first term, the expected utility for picking low rents and high rents respectively are given by U(L)=E+ µ L + β p L (E+ µ H γ) U(H)=E+ µ H γ+ β p H (E+ µ H γ) where E are ego rents net of the outside option, β is the discount factor, p L P(reelection L) is her probability of reelection if she picks low rents in her first term, and p H P(reelection H) is her probability of reelection if she picks high rents in her first term. Let the probabilities p L and p H be taken as given for now, as they will be equilibrium outcomes. Hence, a dissonant incumbent chooses to extract low rents in her first term if and only if γ µ H µ L β(e+µ H )(p L p H ) 1 β(p L p H ). We denote by λ the probability that a dissonant incumbent extracts low rents, or equivalently, the probability that a dissonant politician pools with the congruent politicians. Thus the probability is given by ( ) µh µ L β(e+ µ H )(p L p H ) λ = 1 F γ 1 β(p L p H ) (1) The voter s problem We assume that there is a representative voter. The voter observes a noisy signal of the rents extracted by the politician with probability χ. Rents are revealed imperfectly with a noise term ε N(0,σ 2 ), such that the voter either observes a draw from r L N(µ L,σ 2 ) if the incumbent chose low rents or a draw from r H N(µ H,σ 2 ) if the incumbent chose high rents. We let f L and 10

12 f H denote the respective density functions. The voter also observes the incumbent s popularity shock δ, which is drawn from a distribution F δ after the incumbent picks her action. The popularity shock enters the voter s utility function linearly. After observing the popularity shock and (possibly) the rents that were extracted, the voter chooses whether to reelect a first-term incumbent or select a challenger who is drawn at random from the pool of potential politicians. The voter will choose to reelect the incumbent if the voter s expected utility for reelecting the incumbent exceeds his expected utility for choosing a random challenger. Denote by ˆπ(r) the voter s belief of the probability that the incumbent is a congruent type, which may depend on the realized rent r. Taking the voter s belief as given, the voter will reelect the incumbent if: ˆπ(r)µ L +(1 ˆπ(r))µ H + δ V n where δ is the incumbent s popularity shock and V n is the expected utility from a new challenger. Since the value of a challenger is given by V n = πµ L (1 π)µ H, we find that the incumbent s probability of reelection given a realized rent r is: P(reelection r)=1 F δ [(µ H µ L )(π ˆπ(r))] (2) Timing of the game To recap, the timing of the game is as follows: 1. The type (congruent or dissonant) and cost of extraction γ are realized and are privately observed by the incumbent. 2. The incumbent chooses high rents or low rents, i.e. an action from {H,L}. 3. A noisy signal of the rents r is observed by the voter with probability χ. The incumbent s popularity shock δ is realized and is observed by the voter. 4. Elections are held. 5. If reelected, the incumbent chooses to extract high or low rents. Otherwise, a randomly chosen candidate is selected, observes her type, and makes her rent extraction choice. 11

13 Equilibrium We solve for the Perfect Bayesian Nash Equilibrium. We first solve for the voter s posterior belief ˆπ(r). If the voter observes the rents signal r, the voter s posterior belief that the incumbent is congruent is given by Bayes rule: f(r congruent)p(congruent) P(congruent r) = f(r congruent)p(congruent) + f(r dissonant)p(dissonant) f L (r)π = f L (r)π+[f L (r)λ + f H (r)(1 λ)](1 π) However if the voter does not observe the level of rents, he will stick to his prior π. Therefore, when the incumbent decides whether to extract high or low rents, she expects the voter to update her belief to ˆπ(r) = f L (r)π χ+ π(1 χ) (3) f L (r)π+[f L (r)λ + f H (r)(1 λ)](1 π) We can now solve for p H and p L, the ex ante expected probability that the incumbent is reelected if she chooses to extract high or low rents respectively. To do so, we integrate (2) over the appropriate density function: p H = P(reelection r) f H (r) dr (4) p L = P(reelection r) f L (r) dr (5) The equilibrium values of p L and p H are given by solving (4) and (5) simultaneously. The remaining equilibrium outcomes follow immediately. The Effect of Audits In this section, we will consider the channels through which audits may affect corruption, which we measure by expected rents in the model. More precisely, suppose that in period 1, the incumbent is 12

14 randomly selected from the pool of candidates. The expected rents in periods 1 and 2 are given by: R 1 =[π+(1 π)λ]µ L +(1 π)(1 λ)µ H R 2 = π p L µ L +(1 π)(λ p L +(1 λ)p H )µ H +[(π+(1 π)λ)(1 p L )+(1 π)(1 λ)(1 p H )]µ n where µ n πµ L +(1 π)µ H is the expected rent accrued by a random challenger selected in period 2. We will suppose that the experience of an audit may increase any of the parameters χ, γ and π, each of which will affect corruption in different ways. A higher probability of detection, first, will discipline some first-term mayors to extract low rents and, second, will alter the selection of mayors that are reelected. Third, an increase in the expected costs of rent extraction, whether due to reputation, legal or other reasons, will decrease rents extracted in both periods. Finally, an increase in the share of congruent candidates who run for mayor will also reduce rents in both periods. We henceforth refer to these four channels as the discipline, selection, reputation and entry effects, which we next analyze in turn. Political Selection and Discipline Consider an increase in χ, the probability that rents are revealed to the voter. We interpret the parameter χ as the sum of two probabilities: namely, the probability of being audited times the probability of detecting corruption conditional on the audit, plus the probability of detection through other means. Even if the objective probability of being audited is constant across municipalities within a state, the experience of an audit can affect an incumbent s perception of detection. 6 A change in χ will have two effects: it will have a disciplining effect which reduces period 1 expected rents, and a selection effect which will have an ambiguous effect on period 2 expected rents. Period 1 expected rents change by: R 1 χ = (1 π)(µ H µ L ) λ χ < 0 where λ χ > 0 because an increase in the probability of revelation will increase p L p H, the difference in the reelection probability between choosing low rents and high rents. Therefore the disciplining effect will always reduce period 1 expected rents. (2011). 6 This interpretation is common in the literature examining the effects of tax audits. See for example, Kleven et al. 13

15 Consider the change in period 2 expected rents due to an increase in χ: R 2 χ = π p L χ (µ n µ L )+(1 π) p H χ (µ H µ n )+ [ (1 π) λ (p L p H ) + λ ] χ χ (p L p H ) (µ H µ n ) The first term reflects the change in rents due to the change in the probability that congruent types are reelected. The sign of this effect will depend on the sign of p L / χ: rents will be reduced if congruent types are more likely to be reelected following an increase in χ. In general, the sign of this effect will depend on the parametrization of the model. The second term reflects the decrease in rents due to the reduction in the probability of reelection for dissonant incumbents who extract high rents. The third term reflects the increase in rents due to dissonant types pooling more often and being reelected more often when χ increases. Thus the direction of the overall selection effect is ambiguous. Reputation The experience of an audit may cause a mayor to update her beliefs about the expected costs which result from an audit revealing high levels of corruption. The expected costs in this case are distinct from the electoral costs which we capture by χ above. These may include reputation, legal and other costs. For simplicity, we refer to the effect of this channel on rents as the reputation effect. Let the distribution of costs be uniform. Then each dissonant mayor observes a type γ drawn from the distribution U[0, µ H µ L ]. Now suppose that the experience of an audit causes the cost of high rent extraction to increase from γ to γ+ κ, for some κ c(µ H µ L )>0. In this case, the share of mayors extracting low rents in both terms increases from π to π+ c. The increase in the share of mayors who extract low rents in both periods leads to a first-order decrease in expected rents in both periods. It also leads to a second-order effect on rents through a change in the reelection probabilities p L and p H, which affects the number of pooling mayors in the first period and the selection of mayors in the second period. 14

16 Entry An increase in the share of congruent mayors, π, will have similar implications to an increase in the cost of rent extraction. The first-order effect will be a decrease in rents extracted in both terms since the share of mayors who extract low rents in both terms increases. A change in π will also have a second-order effect through a change in the reelection probabilities p L and p H, which affects the share of pooling mayors in the first period and the selection of mayors in the second period. We refer to the total change in rents as the entry effect. 4 Research Design We are interested in testing whether audits reduce future corruption. To test this hypothesis, we need to overcome the fact that we only observe corruption once a municipality has been audited. We do so by exploiting municipalities that have been audited multiple times. As we see in Figure 3, out of the 2241 municipalities that have been audited, 25 percent of them have been audited multiple times: 506 audited twice, 54 three times, and 4 municipalities 4 times. As a result, for a given round of audits, we can compare the corruption levels of municipalities that had been audited prior to this audit to those that had not (and are thus being audited for the first time). Figure 4 shows the main variation we will exploit. The first time a municipality was audited for a second time occurred in the 11 th lottery. As expected, the number of municipalities that have been audited more than once increases over time. For instance, in the 30 th lottery out of the 60 municipalities audited, 19 had been audited in the past. Note that because the lotteries are conducted at random, for a given lottery at time t the probability that a municipality has been audited in the past is the same for all municipalities within a particular state. Given this structure of the data, we estimate the following model for municipality m in state s, audited at date t. Corruption mst = α+ βpast Audit mst + X msγ+ f(nos) mst + ν s + δ t + ε mst (6) where Corruption mst is the amount of corruption detected in municipality m during audit t, and Past Audit mst is an indicator for whether at date t the municipality had been audited in the past. The vector X ms consists of a set of municipal characteristics (e.g. population, income per capita, income inequality, etc.) measured in These controls allow us to account for any socioeconomic differences across municipalities prior to the start of the program. The variable nos mst denotes the number of service orders that auditors were sent to investigate. Since audits with more 15

17 service orders tend to discover more irregularities, it is important to account for these differences in a flexible manner. In our preferred specification, the number service orders is control for completely non-parametrically. The error term, ε mst, captures unobserved (to the econometrician) determinants of corruption. Importantly, our model also adjusts for two classes of fixed-effects. We include state intercepts, ν s, to capture the fact that the randomization is stratified by state. 7 We also include lottery fixed effects, δ t, which is important for two reasons. First, although municipalities are more likely to become treated over time, within a given lottery, the probability that a municipality had been audited in the past is the same for municipalities within the same state. Second, and more importantly, starting in the 20 th lottery, the CGU began to audit funds in selected areas and programs. As a result, it is difficult to compare corruption levels over time, and hence we restrict our analysis to variation within audits. Because municipalities are audited at random, we can interpret the coefficient β as the causal effects of the audits on corruption. In addition to estimating the these average effects, we also test whether the effects vary according to characteristics of the municipality. In this case, we estimate the following specification: Corruption mst = α+ βpast Audit mst + θpast Audit mst (Z ms E[Z ms ])+X msγ + f(nos) mst + ν s + δ t + ε mst where Z ms is a characteristic of the municipality, also contained in the vector X ms. Testing the Alternative Channels In Section 3, we discussed four reasons why the audits can reduce corruption. The first is a political selection effect among mayors that are eligible for reelection. If the audits allow voters to punish corrupt mayors and reward good ones, then we would expect better politicians in places where the incumbent was audited prior to the election and still re-elected. The second channel is a discipline effect. If the audits change the perceived probability of being found to be corrupt, then mayors who have re-election concerns will refrain from corruption. The third channel is what we have termed a reputation effect. Mayors who have been audited in the past may refrain corruption even absence re-election incentives, lest they incur reputation (or legal) costs. The fourth channel is an entry 7 Given the population density of North Brazil, when CGU draws municipalities for audit, this region, which includes the states of Acre, Amapá, Amazonas, Pará, Rondônia, Roraima and Tocantins, is treated as a single state. 16

18 effect. If the audits induced more congruent types to enter into the candidate pool, then this could also lead to a reduction in corruption. To test these alternative channels, we consider 5 groups of municipalities: 1. Experienced an audit: Municipality in which the incumbent experienced two audits within the same term. 2. Audited t 1 &Reelected t : Municipality was audited at t 1 and the incumbent was reelected at t. 3. Audited t 1 &New Mayor t : Municipalities that were audited and the incumbent was not reelected. 4. Not audited t 1 &Reelected t : Municipality was not audited t 1 in the past and the incumbent was reelected. 5. Control: Municipality has not been audited Discipline and Reputation Effects. Based on these groups, consider the following regression: Corruption mst = α+ β 1 1[Experienced an audit] mst + β 2 1[Audited t 1 &Reelected t ] mst (7) + β 3 1[Audited t 1 &New Mayor t ] mst + X msγ+ f(nos) mst + ν s + δ t + ε mst where the 1[ ] is an indicator for belonging in the specified group. The omitted group represents the municipalities that have not been audited (i.e. 1[Control] 1[Not audited t 1 &Reelected t ]). The municipalities indicated by 1[Experienced an audit] represent cases in which a mayor experiences an audit early in his term (often over funds that he had not administered), and is then effectively audited again in the same term. 8 Since these are situations in which an election has not occurred, the difference in corruption levels between these municipalities and the omitted group, β 1, can only be due to either a discipline effect and a reputation effect. To these further distinguish between these two effects, we can these effects vary by whether or not the mayor was in his second term. Because second-term mayors are term-limited, they should only respond due to reputational 8 Note that the audit may have even occurred in the subsequent term, but the funds audited referred to those administered under the previous term. 17

19 concerns. In other words, we estimate the following equation: Corruption mst = α+ β 1 1[Experienced an audit] mst (8) + φ(1[experienced an audit] mst Second term mst ) + β 2 1[Audited t 1 &Reelected t ] mst + β 3 1[Audited t 1 &New Mayor t ] mst + X mstγ+ f(nos) mst + ν s + δ t + ε mst where Second term mst is an indicator for whether the mayor is in his second term. In specifying this equation, we are assuming that Second term mst is also contained in the vector of controls X mst. Based on this specification, the differential effect between first and second-term mayors, φ, will capture a discipline effect. The combination of β 1 + φ will measure a reputation effect. Political Selection. The effects of political selection on corruption in period 2 comes from both an increase in the probability that a congruent type gets re-elected, as well as a decrease in the probability that a dissonant type get re-elected. Thus, to test the existence of political selection, we can compare mayors that were audited and re-elected to mayors who were not audited but were also re-elected. This difference in corruption levels will reflect the change in the composition of mayor types (political selection) as well as a reputation effect, which given our estimate of equation 7 we can net out. Specifically, we estimate the follow equation: Corruption mst = α+ β 1 1[Experienced an audit] mst (9) + φ(1[experienced an audit] mst Second term mst ) + β 2 1[Audited t 1 &Reelected t ] mst + β 3 1[Audited t 1 &New Mayor t ] mst + β 4 1[Not audited t 1 &Re-elected t ] mst + X msγ+ f(nos) mst + ν s + δ t + ε mst where the 1[Not audited t 1 &Re-elected t ] mst is an indicator for municipalities that were not audited at t 1, but the mayor was re-elected at time t. Note that the omitted group in this specification represents just the control municipalities. Based on this model, we can test for political selection by estimating β 2 β 3 (β 1 + φ). Political Entry. A fourth channel through which the audits may have affected corruption is political entry. This would be the case if the audits affect the types of politicians that run for office. We test for comparing corruption levels in places that were audited at t 1 to those that were not, conditional on having a new mayor in time t a difference which by estimated by β 3 in Equation 18

20 9. 9 Conditional on having a new mayor at time t, there are three effects that could be driving this difference: a discipline effect, reputation effect, and a political entry effect. With estimates of the first two effect, we can easily net out the political entry effect. Alternatively however, because the audits occurred during the previous administration, new mayors may not have necessarily updated their subjective probabilities on the probability of being revealed. In which case, β 3 alone would provide a simple test of political entry. 5 Results 5.1 Reduced-form Estimates Effects of the Audits on Active and Passive Waste Table 3 presents OLS regression results from estimating several variants to Equation 6. The specification in the first column estimates the effects of having been audited on the total number of irregularities discovered in the audit, controlling for state and lottery intercepts, as well as the number of service orders. Column 2 extends this specification in Column 1 to include various socio-economic characteristics of the municipality. Our preferred specification is presented in Column 3, which modifies the specification in Column 2 to control for the number of service orders in a nonparametric manner. The results in columns 1-3 suggest that municipalities that had been audited in the past commit significantly fewer irregularities than those that had not been previously audited. Once we control for municipal characteristics and service-order fixed-effects, we estimate a reduction of 4.3 percent. We also find that the number of irregularities correlates with several of characteristics we have come to expect from the cross-country literature. For example, we see strong negative associations with income per capita and literacy rates, as well as positive correlations with income inequality and population. As we have discussed above, there is an important distinction to be made between active and passive waste, and we do this in columns 4-9. In columns 4-6, we replicate the specifications presented in 9 Note that there are two reasons this could occur: either the incumbent was not re-elected or the incumbent mayor was already in his second term (i.e. the election was over an open seat). We decided to group these two types of municipalities because we do not find differential effects by whether the new mayor was based on an open seat election. 19