Political Information Cycles: When Do Voters Sanction Incumbent Parties

POLITICALINFORMATIONCYCLES: WHEN DO VOTERS SANCTION INCUMBENT PARTIES FOR HIGH HOMICIDE RATES?∗

JOHN MARSHALL†

APRIL 2018

I argue that voter news consumption tracks electoral cycles, and thus electoral accountability is often shaped by noisy performance indicators revealed before elections. Examining local homicides prior to Mexican municipal elections, I test this theory’s central implications using three sources of plausibly exogenous variation. First, I show that voters indeed consume more news and are better informed before local elections. Second, pre-election homicide spikes substantially decrease the incumbent party’s re- election prospects. Sanctioning is limited to mayors controlling local police forces, and does not reflect longer-term homicide rates. Third, the punishment of pre-election homicide shocks increases with access to local broadcast media stations. Such political information cycles appear to reflect poorly-informed Bayesian voters demanding more information during election campaigns, rather than naive responses to exogenous adverse events. By highlighting the importance of when voters consume news, these findings can help explain variation in the media’s political influence and the mixed evidence that information supports electoral accountability.

JEL codes: D72, D78, O17.

∗I thank Jim Alt, Eric Arias, Abhijit Banerjee, Allyson Benton, David Broockman, Bruce Bueno de Mesquita, Melani Cammett, Francisco Cantu,´ Ana De La O, Oeindrila Dube, Raissa Fabregas, Nilesh Fernando, Hernan´ Flom, Alex Fouirnaies, Jeff Frieden, Thomas Fujiwara, Saad Gulzar, Sebastian Garrido de Sierra, Andy Hall, Torben Iversen, Joy Langston, Horacio Larreguy, Chappell Lawson, Sandra Ley, Rakeen Mabud, Noah Nathan, Brian Phillips, Carlo Prato, Otis Reed, James Robinson, Rob Schub, Gilles Serra, Jim Snyder, Chiara Superti, Edoardo Teso, Giancarlo Vis- conti, Julie Weaver, and workshop or conference participants at presentations at APSA, Berkeley, Caltech, Columbia, Harvard, LSE, MIT, MPSA, NYU, NEWEPS, Stanford, Stanford GSB, and Yale for illuminating discussions and useful comments. I thank Horacio Larreguy for kindly sharing municipal election data. †Department of Political Science, Columbia University. Email: [email protected].

1 1 Introduction

Electoral accountability ideally supports effective governance that increases voter welfare by enabling informed voters to select suitable politicians to represent them. Given the difficulty of directly observing an incumbent’s competence or alignment with voter interests, performance on salient issues like economic growth, redistribution, public security, or corruption can serve as valu- able signals of an incumbent’s continuing suitability for office (Fearon 1999; Rogoff 1990). How- ever, particularly in developing contexts, voters are often poorly informed about politics and current affairs (e.g. Keefer 2007; Pande 2011), or do not receive relevant information pertaining to their incumbent party (Larreguy, Marshall and Snyder 2018; Snyder and Stromberg¨ 2010).1 This lack of politically-relevant information may explain why voters often fail to hold incumbents to account for their performance in office (e.g. Dunning et al. forthcoming).2 In response, scholars and policymakers have argued that increasing access to media can facilitate electoral accountability. This rests on media outlets deciding to report relevant incumbent performance indicators that voters would not otherwise obtain, and receives some empirical support (see Ashworth 2012; Pande 2011).3 Although this may be a precondition for accountability, the focus on access neglects the reality that the availability of media coverage does not necessarily imply that voters actually consume politically-relevant news. I argue that how voters hold incumbent parties to account for their performance in office also reflects the timing of their news consumption. News consumption is likely to track electoral cycles if, before elections, voters actively seek out politically-relevant information (e.g. Feddersen and San- droni 2006; Hamilton 2004; Marshall forthcoming) or media outlets increase their supply of such information. Consequently, incumbent performance indicators reported by media outlets before elections—when voters consume most news—have the potential to disproportionately influence election outcomes, especially in low-information environments where voters possess imprecise prior beliefs. Such political information cycles could help account for the apparently large impact of the revelation shortly before the 2016 U.S. presidential election that the FBI was continuing to investigate Hillary Clinton.

1Ill-informed electorates also pose similar dilemmas in established democracies (Delli Carpini and Keeter 1996), but the risks of electing incompetent politicians are likely greater under weak democratic institutions. 2Evidence that voters in consolidating democracies punish or reward politicians for economic performance (An- derson 2007; Remmer 1991; Roberts and Wibbels 1999), levels of public security (Vivanco et al. 2015), or malfeasance in ofﬁce (Arias et al. 2018; Chong et al. 2015; de Figueiredo, Hidalgo and Kasahara 2013; Ferraz and Finan 2008; Larreguy, Marshall and Snyder 2018) is mixed. 3Well-identiﬁed studies show that media programming affects voting behavior (e.g. DellaVigna and Kaplan 2007; Enikolopov, Petrova and Zhuravskaya 2011; Larreguy, Marshall and Snyder 2018; Martin and Yurukoglu 2017; Snyder and Stromberg¨ 2010).

2 While voting behavior is likely to be sensitive to informative signals of incumbent type (e.g. Rogoff 1990), even pre-election performance signals that are uncorrelated with desirable characteristics could affect incumbent electoral prospects. Responses to the latter type of signal—this paper’s empirical focus—could reflect rational or irrational belief updating. On one hand, Bayesian voters with limited political information may rely on signals that reflect both performance-relevant characteristics and random shocks (e.g. Ashworth 2005), or learn about the incumbent’s type from their response to the shock (Ashworth, Bueno de Mesquita and Friedenberg forthcoming; Besley and Burgess 2002). On the other, voters could engage in a naive response to adverse pre-election shocks (e.g. Achen and Bartels 2017; Wolfers 2007; Zaller 1992). This paper examines the extent to which political information cycles drive voting behavior in the context of Mexican voters holding municipal incumbent parties to account for local homicides. Following significant democratizing and decentralizing reforms in the 1990s, Mexican elections have become competitive at national and sub-national levels, while responsibility for public service delivery such as policing is increasingly assigned to municipal, rather than state or national, governments. Public security is a major concern for Mexican voters, as in other Latin American nations, and thus local homicides represent a salient measure of incumbent party performance.4 Moreover, since many voters are poorly informed about politics and a significant portion of the electorate lacks strong partisan ties (Chong et al. 2015; Greene 2011; McCann and Lawson 2003), there is scope for crime reports to influence voting behavior. Leveraging plausibly exogenous variation in temporal proximity to local elections, municipal- level homicide spikes occurring before elections, and then access to local broadcast media stations, I test the key features of the political information cycles argument at the individual and aggregate levels. First, to demonstrate the existence of cycles in political news consumption, I exploit the irregular timing of survey waves with respect to Mexican states’ staggered electoral cycles to iso- late variation in the proximity of local—municipal and state legislative—elections (see also Eifert, Miguel and Posner 2010). Rather than separate supply and demand explanations for information consumption, this analysis identifies consumption cycles in equilibrium. I indeed find that voters report consuming more political news through radio and television in the months preceding local elections. For some less-informed voters, they effectively only consume political news during elections campaigns. These changes are reflected in a 0.2 standard deviation increase in topical political knowledge. Second, using electoral returns from between 1999 to 2013, I show that spikes in the inci-

4Although municipal mayors could not seek re-election until 2018, voters generally hold the incumbent’s party responsible for performance in Mexico’s party-centric system (e.g. Arias et al. 2018; Chong et al. 2015; Larreguy, Marshall and Snyder 2018).

3 dence of homicides just before elections—when voters consume most news—substantially harm the municipal incumbent party’s electoral performance.I estimate the effects of these pre-election homicide shocks by leveraging plausibly exogenous month-to-month volatility in homicide counts within municipalities to capture idiosyncratic short-term deviations from longer-term trends. Specif- ically, I compare “shocked” municipal elections that experienced more homicides in the two months preceding the election to “control” elections from within the same municipality that experienced at least as many homicides in the two months after the election.5 I support the design by demonstrating that the distribution of homicide shocks is consistent with random sampling variability, is balanced over 99 predetermined covariates, and inconsistent with manipulation by politicians or drug trafficking organizations (DTOs). Despite being uncorrelated with broader homicide levels and trends, pre-election homicide shocks reduce the incumbent party’s probability of winning by 12 percentage points. Such punishment is consistent with Bayesian and naive responses to noisy signals of incumbent competence. Furthermore, consistent with poorly-informed voters relying on the pre-election signals available when they actually consume news, voters do not hold incumbents accountable for longer-run homicide rates. Using a difference-in-differences design, I find no evidence to suggest that homicide rates over the prior year or electoral cycle—arguably, more desirable indicators of incumbent performance (Healy and Lenz 2014), but which may not be observed by voters predominantly consuming information just before elections—affect incumbent electoral performance. Moreover, my analysis of concurrent state and federal elections, and comparisons between municipalities with and without their own police force, indicate that the parties of incumbent mayors, rather than higher levels of government, are held to account for local homicide shocks (Vivanco et al. 2015). Third, I link the individual and aggregate-level findings by showing that local broadcast media plays a crucial role in linking news consumption to electoral sanctioning. Local broadcasters report politically-relevant news that voters may not be able to access otherwise, and local crime receives substantial media coverage (e.g. Osorio 2015; Trelles and Carreras 2012). Using detailed coverage maps for every radio and television station in the country, I leverage within-neighboring precinct variation in signal access to identify the effects of broadcast media in more urban areas (see also Larreguy, Marshall and Snyder 2018). On average, I find that each additional local media station based within a precinct’s own municipality reduces the incumbent party’s vote share by 0.2 percentage points. However, the 21% of precincts covered by less than 8 local media stations do not significantly punish homicide shocks. Neither additional non-local media stations nor party ad shares on accessible outlets can account for these findings.

5I include only municipalities experiencing at least one homicide over the two months before and after an election.

4 Turning to the mechanisms, the observed electoral sanctioning is consistent with voters demanding more news before elections and updating from the events in the news at this time in a Bayesian fashion. First, indicating that voters internalize news in the media just before elections, pre-election homicide shocks both increase concern about public security and reduce confidence in the municipal incumbent by around 10 percentage points. In contrast with a “recency bias” ex- planation, homicide shocks occurring before surveys outside of electoral campaigns—when voters consume less news—do not significantly influence voter beliefs in the short term. Second, il- lustrating voters’ capacity to integrate new information with their prior beliefs, the sanctioning of homicide shocks is greatest where a different incumbent party at the previous election did not over- see a pre-election homicide shock, or the same incumbent party experiences consecutive shocks. Such sophistication suggests that naive responses to shocks do not drive the results. Third, I show that although media coverage of violent crime closely tracks the occurrence of homicides, coverage does not increase during election campaigns. In conjunction with the fact that some voters only consume news before elections, this suggests that demand for politically-relevant news is the primary force underpinning political information cycles. The overarching finding that political information cycles induce voters to heavily weight recent performance indicators makes several contributions. First, the findings extend the literature doc- umenting the persuasive effects of broadcast media content (e.g. Adena et al. 2015; DellaVigna and Kaplan 2007; DellaVigna et al. 2014; Enikolopov, Petrova and Zhuravskaya 2011; Larreguy, Marshall and Snyder forthcoming; Martin and Yurukoglu 2017; Spenkuch and Toniatti 2016; Yanagizawa-Drott 2014), and especially the importance of local news (Ferraz and Finan 2008; Larreguy, Marshall and Snyder 2018; Snyder and Stromberg¨ 2010). In contrast with these studies focusing on access to media at particular points in time, I demonstrate that the effects of the media vary systematically with the timing of voter news consumption. I thus highlight the importance of consumption patterns for understanding the broader effects of editorial content and coverage of particular events. Second, integrating cyclical news consumption into models of electoral accountability helps account for the mixed evidence that incumbent performance information influences voting behavior. For example, the timing of information consumption may explain why pre-election corruption revelations have produced larger electoral impacts than similar revelations occurring earlier in a electoral cycle (Brollo 2009; Chang, Golden and Hill 2010), voters tend to overweight recent economic performance in evaluating U.S. presidents at the end of their term (Achen and Bartels 2017; Healy and Lenz 2014), and short-term fluctuations have induced electoral volatility across Latin America (Roberts and Wibbels 1999). Furthermore, the importance of local media coverage in my

5 findings reiterates the substantially larger effects associated with media dissemination of incumbent performance information (Banerjee et al. 2011; Ferraz and Finan 2008; Keefer and Khemani 2014; Larreguy, Marshall and Snyder 2018) relative to dissemination campaigns that provide information to voters in person (e.g. Chong et al. 2015; de Figueiredo, Hidalgo and Kasahara 2013; Dunning et al. forthcoming; Humphreys and Weinstein 2012). Nevertheless, the previous findings that local media can induce and amplify electoral sanctioning focus on revelations occurring shortly before elections. This paper thus tempers the media’s pro-accountability potential by il- lustrating the importance of timing information dissemination campaigns to coincide with voter engagement. Third, the evidence further illuminates the process through which voters process information and update their beliefs. Rather than responding naively to exogenous adverse shocks, voter beliefs and behavior—which reflect positive and negative pre-election homicide shocks, are differen- tiated across mayors with and without a police force, and vary with previous pre-election homicide shocks experiences—is consistent with Bayesian updating in a career concerns model or from evaluating responses to random shocks. These findings complement the sophisticated updating documented by field experiments in both developed (Kendall, Nannicini and Trebbi 2015) and developing contexts (Arias et al. 2018; Banerjee et al. 2011), but do so in the context of violent crime—a metric of incumbent performance that has received limited empirical attention, despite representing a key valence issue in many developing contexts.6 Nevertheless, in line with Durante, Pinotti and Tesei(2017), the results also highlight the substantial degree to which the behavior of voters with limited information can be influenced by media reporting on noisy signals of incumbent performance. Finally, the importance of political information cycles contributes to a broader political economy literature emphasizing cyclical political behavior and outcomes. Previous studies have observed that economic policies and output (e.g. Brender and Drazen 2005), the distribution of aid (Faye and Niehaus 2012), and corruption levels (Bobonis, Fuertes and Schwabe 2013) reflect an- ticipated electoral cycles. My findings similarly chime with the strategic decision of politicians to act surreptitiously when the media is covering other major events (Durante and Zhuravskaya forthcoming; Eisensee and Stromberg¨ 2007). In contrast with such cycles driven by the actions of politicians, I show that cyclical behavior primarily driven by voters can also have important electoral implications. These news consumption cycles mirror, and could induce, the cycles in partisan

6Existing studies use less plausible identiﬁcation strategies and do not address political information cycles (Vi- vanco et al. 2015). Other studies examine the effects of terrorism (Berrebi and Klor 2006) or the effects of crime solely on beliefs and ratings (Arnold and Carnes 2012), political participation (Bateson 2012; Ley 2014), or trust (Blanco 2013; Corbacho, Philipp and Ruiz-Vega 2015).

6 identiﬁcation observed across the world (Michelitch and Utych 2018). The paper proceeds as follows. Section2 considers sources of political information cycles, and the implications for electoral accountability. Section3 describes the Mexican context used to test the argument. Sections4-6 examine three central components of political information cycles: the timing of information consumption, the effect of homicides occurring at different points on incumbent electoral performance, and the moderating role of media coverage. Section7 evaluates mechanisms.Section8 concludes by discussing broader implications.

2 Theoretical framework

Electoral accountability is underpinned by voters re-electing competent or aligned incumbent parties on the basis of relevant performance indicators (Fearon 1999; Maskin and Tirole 2004; Rogoff 1990). In light of the mixed evidence that voters use performance information to hold incumbents to account (see e.g. Anderson 2007; Ashworth 2012; Healy and Malhotra 2013; Pande 2011), scholars have emphasized the importance of voter access to politically-relevant news in the media (Ferraz and Finan 2008; Larreguy, Marshall and Snyder 2018; Snyder and Stromberg¨ 2010). How- ever, such studies assume that voters actually consume the available information. Furthermore, by focusing on performance metrics released before elections, extant research has failed to capture how the timing of when news is released may differentially affect voter beliefs and behavior. I instead propose that the impact of news on electoral accountability depends upon the timing of voter news consumption. Speciﬁcally, I suggest that news consumption follows a cycle where many voters only seriously encounter politically-relevant information—performance indicators pertaining to incumbents that a voter can sanction electorally—just before elections. Voters thus rely on the incumbent performance indicators in the news at this time when casting their ballot, which are often noisy signals of incumbent competence or alignment with voter interests.

2.1 Causes of political information cycles

Voters seeking to inﬂuence outcomes of mass elections generally face strong incentives to remain “rationally ignorant” (Downs 1957). However, there are a number of reasons to believe that consumption of politically-relevant news increases before elections. First, to the extent that political news is a consumption good (e.g. Baum 2002; Hamilton 2004), electoral campaigns are likely to particularly engage voters. While coverage of political events out of election season is often more focused on speciﬁc policy issues, dramatic campaigns appeal toa broader audience (e.g. Farnsworth and Lichter 2011).

7 Second, voters may acquire political information before elections for strategic reasons beyond affecting election outcomes. Marshall(forthcoming) shows that voters in social networks that col- lectively value knowledge about politics acquire information about election campaigns to cultivate a reputation as politically sophisticated. Such dynamics may be especially strong around elections when political discussion is more common (Baker, Ames and Renno 2006). Similarly, voters may acquire information ahead of elections to improve decision-making in other domains (Larcinese 2005), e.g. if investment choices depend upon political risks. The information consumed for such social and vocational reasons may spill over to influence vote choices. Third, voters may feel a civic duty to become informed around elections. Feddersen and San- droni(2006) argue that “ethical” independent voters are intrinsically motivated to cast an informed ballot, where information acquisition is concentrated among voters facing the lowest acquisition costs. A large body of research suggests that a voter’s civic duty is correlated with political engagement and participation (e.g. Blais 2000). Relatedly, Degan(2006) suggests that voters acquire information to avoid the psychic costs of voting for non-preferred candidates. Fourth, voters without instrumental or intrinsic motivations may still consume more information around elections simply because more time and space is devoted to political news, advertising, and specific election programming. Even for uninterested voters, such information becomes dif- ficult to avoid—especially where there are relatively few channels available (Prior 2007) or such information is recast as entertainment (Baum 2002)—and performance indicators are increasingly placed in the context of appraising incumbent politicians and parties (Semetko and Valkenburg 2000). Regardless of whether consumption is driven principally by voter demand for information or media supply of information, consumption of politically-relevant news is thus likely to increase prior to elections. Such political information cycles would cause many voters—especially in developing contexts where baseline political knowledge is comparatively low (Keefer 2007; Pande 2011)—to essentially engage with the news before the election for the first time in an electoral cycle. Relatively politically engaged voters are, in turn, likely to ratchet up their exposure to political news.

2.2 Consequences for electoral accountability

Provided that voters can access credible news (e.g. Chiang and Knight 2011) and wish to use incumbent performance indicators to elect better politicians (e.g. Arias et al. 2018; Krosnick and Kinder 1990), political information cycles may affect electoral accountability by inducing voters to respond to politically-relevant information when news consumption is greatest before elections.

8 For example, if there are many homicides in the local news just before an election, voters may become more concerned about public security and negatively update their beliefs about the ability of responsible incumbents to effectively reduce crime once re-elected. Such a response could reflect both naive and sophisticated responses to events in the news. A large literature suggests that voters may respond to political information in a naive manner. Zaller(1992) argues that, among voters that actually consume news without engaging in motivated reasoning, new information has short-lived effects on voter beliefs and vote choices. This is because the political opinions of such voters reflect recent considerations that are neither internal- ized nor critically evaluated. Healy and Lenz(2014) further suggest that voters consciously rely on less accurate signals of economic performance, although others highlight voters’ propensity to over-respond to weak signals (e.g. Ortoleva and Snowberg 2015). These information processing failures appear to influence voting behavior: the findings of Achen and Bartels(2017), Healy, Malhotra and Mo(2010), and Wolfers(2007) suggest that voters sanction and reward incumbents for pre-election events—including shark attacks, local sports team defeats, and macroeconomic fluctuations—that are beyond the incumbent’s control.7 Alternatively, voters whose news consumption patterns track electoral cycles may rationally holds officials to account based on information in the news just before elections. As Appendix A.1.1 shows formally in a simple career concerns model (Ashworth 2005), Bayesian voters may update from events both within and beyond the incumbent’s control. When incumbent performance indicators such as economic growth or crime rates reflect both unobservable incumbent competence and random fluctuations, voters use performance cutoff strategies to sanction incumbents that perform below expectations because they attribute the observed outcome to a combi- nation of both underlying sources of performance outcomes. As voters receive more independent performance signals, by consuming news throughout the electoral cycle, they are able to average across idiosyncratic shocks and more frequently re-elect the most competent incumbents. How- ever, voters that principally consume news before elections only observe a small number of performance indicators, and thus sanction incumbents for poor performance even when such performance partly reflects events beyond the incumbent’s control. Political information cycles may thus induce Bayesian voters to rely on noisy performance indicators revealed before elections. A second channel through which pre-election shocks—even when beyond the incumbent’s control—could rationally induce electoral accountability is if the occurrence of such shocks provides an opportunity for voters to learn about the incumbent’s suitability for office. For instance,

7The ﬁrst two empirical ﬁndings have been challenged by recent re-assessments (Fowler and Hall forthcoming; Fowler and Montagnes 2015).

9 Ashworth, Bueno de Mesquita and Friedenberg(forthcoming) develop a model where voters sanction incumbents after natural disasters when such disasters interact with unobserved incumbent competence, such as disaster preparation. Rather than acting naively, voters will sanction incumbents (with an electoral advantage) on average following a random shock if the shock reveals low competence by amplifying the extent to which competence drives observed performance outcomes. Besley and Burgess(2002) convey similar insights. Appendix A.1.2 also develops a simple signaling model where separating equilibria are characterized by competent incumbents distinguishing themselves in response to a shock (Rogoff 1990), e.g. by appearing empathetic in the media or proposing credible policies to mitigate violence if re-elected, in their response to a homicide shock beyond their control.8 In such a model, a negative shock reduces the incumbent’s vote share on average where there is a large density of weak incumbent supporters—as is often the case in competitive elections—because incumbent vote tallies are more responsive to bad than good news. Consistent with such theories, Cole, Healy and Werker(2012), show that, conditional on a shock occurring, (in)effective policy responses can mitigate (accentuate) the negative consequences of natural disasters. However, even without conditioning on post-treatment responses, these models predict differential responses to shocks beyond the incumbent’s control on average. The following empirical analysis tests the central predictions of political information cycles: whether political news consumption increases before elections; whether adverse events reported in the news before elections inﬂuence electoral accountability, and are driven by access to the media; and ultimately the extent to voting behavior reﬂects naive or Bayesian responses to news. These hypotheses are examined in the context of local homicides in Mexico—an important performance indicator on a salient topic widely reported by local media—ahead of municipal elections.

3 Violent crime and political accountability in Mexico

Despite holding regular elections, Mexico was effectively a one-party state until the late 1990s.9 Mexico has since democratized signiﬁcantly, with competitive elections between three main political parties—the right-wing National Action Party (PAN), left-wing Party of the Democratic Revolution (PRD), and previously-hegemonic Institutional Revolutionary Party (PRI).10 Despite

8In contrast with the career concerns model and Ashworth, Bueno de Mesquita and Friedenberg(forthcoming), this model assumes that incumbents know their own types. 9The PRI had retained a stranglehold on power since 1929 by implementing populist policies, establishing strong clientelistic ties, effectively mobilizing voters, creating barriers to political entry, and manipulating electoral outcomes (e.g. Cornelius 1996; Greene 2007; Magaloni 2006). 10After attaining legislative pluralities in the 1990s, the long-time conservative opposition PAN fully broke PRI control when Vicente Fox won the Presidency in 2000. In 2006, Felipe Calderon´ retained the Presidency for the

10 growing partisan alignment, often induced by clientelistic exchanges, many Mexicans have yet to develop strong ties to specific political parties (Greene 2011; Lawson and McCann 2005). Mexico’s federal system is divided between three administrative and elected layers of government: the federal government, 31 states (and the Federal District of Mexico City), and approximately 2,500 municipalities. Constitutional reforms in the mid-1990s substantially increased mayoral autonomy over the provision of local public services (see Diaz-Cayeros, Gonzalez´ and Rojas 2006), inducing municipal spending to rise to around 20% of total government spending.11 The median municipality contains 13,000 people.Large cities with the exception of the Federal District—which is divided into delegations—represent singular municipal bodies. Municipal mayors have typically been elected every three years to non-renewable terms,12 and entered office between three and seven months after election day. Municipal elections are almost always held concurrently with state legislative elections, although gubernatorial elections are often held separately. I refer to simultaneous municipal and state legislative elections as “local elections.” Such local elections have become increasingly competitive, with fewer than 50% of municipal incumbent parties being re-elected and 31% of elections being won by less than 5 percentage points. The majority of local elections do not coincide with federal elections.13 Many mayors, especially those in large municipalities, seek other elected offices at the end of their term. Although incumbent mayors could not seek re-election, Mexico’s party-centric system ensures that voters are likely to hold incumbent parties accountable for the performance of individual politicians. First, voters primarily decide between party labels, not individual candidates. Arias et al. (2018) report that 80% of voters can identify the party of their municipal incumbent; this far exceeds the probability of correctly naming individual local incumbents (Chong et al. 2015; Lar- reguy, Marshall and Snyder forthcoming). Second, differences in candidate selection mechanisms across parties at the state level ensure that candidate choices are highly correlated within parties (Langston 2003). Third, various studies find that voters hold parties to account for an incumbent’s malfeasance in office (Arias et al. 2018; Chong et al. 2015; Larreguy, Marshall and Snyder 2018).

PAN, narrowly defeating the PRD’s Andres´ Manuel Lopez´ Obrador. After regaining legislative majorities, but never relinquishing regional control (Langston 2003), the PRI candidate Enrique Pena˜ Nieto won the Presidency in 2012. Since 2015, a fourth major competitor—MORENA—has emerged at the national level. 11This expansion of spending included policing, although most municipalities already had their own police forces. Presidents Fox and Calderon´ also increased federal transfers to municipalities for policing in the 2000s (Sabet 2010). 12From 2018, re-election will become possible for legislators, and mayors in most states. 13House and Senate elections are held every three years, while the President is elected every six years.

11 3.1 Public security forces

Responsibility for public security is shared across levels of government, and like other federal systems such as the United States, mayors play an important role in fighting crime. Both state and federal laws can be used to prosecute criminals, and uniformed (preventive) and investigative police forces exist at both the federal level and in each of Mexico’s 31 states and the Federal District of Mexico City. State and federal police, and increasingly the army, are responsible for investigating major crimes in different jurisdictions. State police investigate state crimes such as homicides, while federal officers focus on organized crime (Reames 2003). However, around three- quarters of municipalities also possess their own police force. Municipal forces support higher- level operations and supply information, but their principal role is preventive: they primarily patrol the streets and maintain public order, address administrative issues, and respond first to criminal incidents (Reames 2003; Sabet 2010).14 Municipal police are by far most numerous, accounting for more than half of Mexican enforcement personnel (Sabet 2010). In municipalities with their own police force, mayors can influence the medium-term incidence of crime. Mayors choose the local police chief and set local policies. PAN mayors have played a key role in supporting Calderon’s´ crackdown on Mexico’s DTOs (Dell 2015), while political alignment across neighboring municipalities has reduced rates of violent crime (Durante and Gutierrez 2015). The widely-publicized case of Iguala represents a particularly egregious example of political control of the local police, where the mayor and his wife exploited their links with law enforcement to cover up and possibly instigate the murder of 43 student protesters in 2014.As shown below, mayors do not manipulate short-term homicide rates. Given the number of municipal police officers and their “on-the-streets” presence, it is not surprising that municipal police are the foremost police force voters’ minds. When asked which types of law enforcement authorities they are aware of, the 2010 National Insecurity Survey (ENSI) finds that while 75% of voters could identify municipal police, only 38% and 48% respectively recognized state and federal forces. Focus groups that I conducted in several large municipalities in 2015 suggest that voters often blame local government for crime in their community.

3.2 Trends in homicide rates

According to the United Nations Ofﬁce on Drugs and Crime (UNODC), Mexico suffers one of the world’s highest homicide rates. In 2011, 22.6 people per 100,000 were intentionally mur- dered. This represents the 20th highest homicide rate in the world—slightly less than South Africa,

14A central police force controlled by the mayor of Mexico City covers all delegations within the Federal District.

12 Calderon's War on Drugs 1.2 .4 1 .3 .8 .6 .2 .4 Average number of homicides .1 .2 1999 2002 2005 2008 2011 2014 Proportion answering that crime is most important 0 Month (January of year) 2001 2002 2003 2004 2005 2006 2007 2008 2009 2010 2011 (a) Trends in monthly homicides (as deﬁned by INEGI) in the average Mexican municipality, (b) Voters listing crime as the most important 1999-2013 problem that Mexico faces, 2001-2011 Figure 1: Crime in Mexico Notes: The data in Figure 1b are from the 2001-2011 Latinobarometro´ surveys. Crime includes concerns about crime/public security, drug trafﬁcking, violence, or terrorism/political violence.

Colombia, and Brazil, and slightly more than Nigeria, Botswana, and Panama. After briefly de- clining since 2011, the 2017 rate will almost certainly be the highest yet recorded. Using data from the National Institute of Statistics, Geography, and Information (INEGI), Mex- ico’s autonomous statistical agency, Figure 1a plots the number of homicides per month occurring in the average municipality between 1999 and 2013. INEGI defines an intentional homicide as an unnatural death, as determined by a coroner’s report.15 The monthly homicide rate has been substantial throughout this period, but increased dramatically after President Calderon´ entered office in December 2006 and began Mexico’s “War on Drugs.” The homicide clearance rate is only approximately 20% (Mexico´ Evalua´ 2012), and drug-related homicides—which are regionally concentrated—represent around half of the homicides over this period (Heinle, Rodr´ıguez Fer- reira and Shirk 2014). However, many municipalities only rarely experience a homicide; in fact, only one homicide occurs in the median municipality each year.

15Month and location of death are also based on the coroner’s report. Although there is no official measure of drug-related homicides enshrined in Mexican law, the federal government has sporadically released monthly data. This data suffers from various problems beyond its short time-series (see Heinle, Rodr´ıguez Ferreira and Shirk 2014), while Dell’s (2015) estimates show that total homicides measured by INEGI rose substantially more than drug-related homicides following Calderon’s´ war on drugs. Furthermore, voter fears about public security are not only linked to organized crime, but also reflect equally-prevalent non-drug related homicides (of which only a tiny fraction occur within families). Table A15 shows broadly similar results for the small sample (December 2006-October 2011) when homicides were classified as drug-related by a committee composed of representatives from the ministries constituting the National Council of Public Security.

13 These ﬁgures could understate the true homicide rate if unnatural causes cannot be detected (Mexico´ Evalua´ 2012). However, it is unlikely that the coroners reports are falsiﬁed because individual-level reports are only released publicly several years after the event. Moreover, 94% of homicides were registered in the same month that they occurred. Unsurprisingly, voters are concerned about Mexico’s high rates of violent crime. Like many other Latin American countries (Blanco 2013), Figure 1b shows that the number of Mexican Lati- nobarometro´ respondents citing public security as the most important problem facing the country increased broadly in line with homicide rates. For most of the 2000s, public security registered as the most salient issue for voters, ahead of the economy.

3.3 Media coverage and voter political knowledge

As in most developing countries, broadcast media is voters’ primary source of news. Accord- ing to the 2009 Latinobarometer, 83% of Mexicans receive political information from television, 41% from radio, 30% from newspapers, and 41% from family, friends, and colleagues. In 2008, around 10% listened to radio every day, while the average person watched 4 hours of television (Ibope/AGB Mexico´ 2009). In contrast, only 21% have access to the internet at home in 2010, while 3G coverage only starting to expand rapidly in 2011.16 Broadcast media coverage thus plays a central role in determining whether voters receive politically-relevant information. Mexico contains 852 AM radio stations, 1,097 FM stations, and 1,255 television stations, which generally cover relatively small geographic areas (see Figure3 below). Most stations form part of broader regional and national radio or television networks—such as Grupo ACIR, Radiorama, Televisa, and TV Azteca—where affiliates share branding or are owned-and-operated subsidiaries (Larreguy, Marshall and Snyder 2018). Among radios, 83% report news more than once a day, and typically report on municipal rather than national issues (Larreguy, Lucas and Marshall 2016). For television stations, identical entertainment content is generally bought from or relayed by network providers. However, while national news is typically centrally provided, affiliates and regional sub- divisions emitting from major cities within each state also provide significant local news content. Of the 52 distinct television channels (excluding Mexico City’s 24-hour news channels) for which schedules were available in 2015, the average channel broadcast 3.6 hours of news coverage each weekday (both before and after the June elections). Slightly less than half of this news is devoted to state- or city-specific programming. Private radio and television outlets rely on advertising rev- enues to support themselves, and thus face strong incentives to tailor their programming to local audiences (Larreguy, Marshall and Snyder 2018). The pro-PRI coverage biases that characterized

16Even in 2010 and 2011, 60% of Latinobarometro´ respondents reported never using the internet.

14 elections before the late 1990s have somewhat dissipated since (e.g. Hallin 2000; Lawson 2002). Homicides are not always reported in great depth, but are regularly covered in print (Ley 2014; Osorio 2015) and are “omnipresent” in the local broadcast media (Trelles and Carreras 2012).17 Based on a survey of all local radio stations conducted in 2016 and 2017 as part of another study (Larreguy, Lucas and Marshall 2016), 96% report regularly covering local security stories, while Table8 below demonstrates that newspaper reporting of violent crime indeed tracks the homicide rate. The 2010 ENSI survey also reports that 87% of respondents learn about public security in the country and in their state from television news programs, while 34%, 29%, and 9% respectively learn from radio news programs, periodicals or newspapers, and the internet.18 Furthermore, 82% of voters believe that television news has the most important influence on public opinion. Despite claiming reasonable levels of attention to political news, voters’ knowledge of public affairs is limited. I show below that only half of Mexicans can answer basic questions about politics. Castaneda˜ Sabido(2011) and Chong et al.(2015) similarly find that voters are generally unaware of mayoral responsibilities and performance in office. This lack of knowledge suggests that many voters may possess weak prior beliefs about their incumbent party’s suitability for office, and may thus internalize information when they actually follow the news.

4 The existence of political news consumption cycles

The political information cycles argument implies that voters consume more political information just prior to elections. While some voters only start consuming politically-relevant information during election campaigns, others will consume more than before. This section ﬁrst estimates the effect of upcoming local elections on such consumption patterns using Mexican survey data.

4.1 Data

I use four cross-sectional waves of the National Survey of Political Culture and Civil Practices (ENCUP) conducted over several weeks in November 2001, February 2003, December 2005, and August 2012.19 The surveys were commissioned by the Interior Ministry and designed to be

17For example, see this local news report of an gangland-style murder in Monterrey. The same news station also reports on domestic murders, e.g. this case of a woman strangling her partner. News programs may continue to report on arrests and the rare cases that go to trial, especially when the defendants are found guilty. 18Although social networks may represent a key source of information on more explicitly political issues (Baker, Ames and Renno 2006), comparatively few learn from work colleagues (5%) or family, friends, and neighbors (13%). 19The study was implemented by INEGI in 2001 and 2003, and private ﬁrms in 2005 and 2012. A 2008 wave was also conducted, but did not provide a respondent’s municipality and asked different media consumption questions.

15 nationally representative, and focus on the country’s political culture rather than more contentious questions about elections.20 Each round draws stratified random samples of around 4,500 Mexican voters for face-to-face interviews from pre-selected electoral precincts within urban and rural strata defined by the electoral register.21 The pooled sample includes up to 17,213 respondents across 539 municipalities (including delegations within the Federal District). Political news consumption is measured in two ways. First, I examine the frequency with which voters report watching or listening to the news, programs about politics, or programs about public affairs.22 To understand the margins at which consumption changes,I distinguish5 consumption intensities: never, at some point, at least monthly, at least weekly, and daily. I code indicators for at least each level above never and a 5-point scale (from 0 to 4). Second, I assess whether self- reported such news consumption translates into greater political knowledge. I focus specifically on topical political knowledge that voters are more likely to encounter through the media (Barabas et al. 2014). Topical political knowledge is measured as the first (standardized) factor from a set of indicators coding correct responses to simple factual questions regarding recent political events and the partisanship of a respondent’s state governor.23 The average respondent answered around half the questions correctly. An advantage of this measure is that voters cannot over-report their knowledge. Because these consumption measures do not differentiate changes in demand for information among voters from changes in the supply of political news provided by media outlets, the results capture equilibrium political information consumption.

4.2 Identiﬁcation strategy

The identiﬁcation strategy leverages the irregular timing of survey waves with respect to state- speciﬁc electoral calendars (akin to Eifert, Miguel and Posner 2010). The timing of ENCUP surveys varies across both the number of years between survey rounds (and thus does not track federal elections) and the month within the year when the survey was conducted, while Mexican states have historically followed different electoral cycles that vary in both the month and year of

20The specific objectives of the study, which does not address elections at all, are enumerated here. 21In 2012, 5 broad strata were identified, and electoral precincts and then voters were randomly selected from within such strata to match the strata’s rural-urban, gender, and age distribution. In 2005 and 2012, 10 voters were surveyed from each precinct according to specific directions (see the 2012 methodological manual here). Although such detailed sampling information is not available for the earlier surveys, the overall design is similar. 22I focus on radio and television, which are by far the most prevalent sources of political information in Mexico. Comparable questions from 2001 were not available. 23In 2001, 2003, 2005, and 2012 respectively, respondents were asked 3, 2, 2, and 2 topical questions (see Ap- pendix). Questions regarding basic knowledge of political institutions were excluded because they are unlikely to be covered directly in the news.

16 their elections.24 Of Mexico’s 32 states (including the Federal District), 27 register an election in one of the survey years, of which 14 only hold an election in a survey year but after the survey occurred. Provided that the surveys were not timed to coincide (or not) with particular elections, whether a survey was administered just before a state’s local elections is plausibly exogenous. Campaigns generally last around 5 months, although there is some variation across states.25 Accordingly, I code an indicator for respondents facing an upcoming municipal election, and typically a simultaneous state legislative election, within5 months of the survey. 26 I then estimate the effect of an upcoming local election using the following regression:

Yimt = βUpcoming local electionmt + µt + εimt, (1)

where Yimt is a measure of political news consumption for respondent i in municipality m at survey year t. Survey fixed effects, µt, control for differences in the difficulty of political knowledge questions across surveys and common period effects that could arise from concurrent federal elections (in 2003 and 2012), Presidential elections (in 2012), or national trends in political behavior. Throughout, standard errors are clustered by municipality. Crucially, there is no evidence to suggest that the ENCUP surveys were strategically timed with respect to local elections. First, Table A2 shows that upcoming local elections are well-balanced over individual and municipal level characteristics: only 1 of 18 tests reports a significant difference at the 10% level. As a robustness check, I control flexibly for the imbalance over respondent education. Second, conditional on a municipality’s inclusion in at least one survey wave, Table A5 shows that neither upcoming local elections nor violence predict whether a municipality is included in any given survey round. Although upcoming local elections are plausibly exogenous to the timing of the survey, I also

implement a difference-in-differences design(by further including state ﬁxed effects, λs) to demonstrate robustness. This design instead relies on the parallel trends assumption that states facing and not facing upcoming elections at the time of the survey follow similar trends in political news con-

24See Table A1 in the Appendix for a full list of municipal elections by month. In Chiapas, Coahuila, Guerrero, Michoacan,´ Quintana Roo, Veracruz, and Yucatan,´ the typical 3-year cycle was adjusted over the sample period by switching to a 2 or 4-year term for a single electoral cycle. Moreover, following a constitutional amendment in 2007, states were subsequently mandated to hold local elections on the same day as federal elections when the state cycle coincides. Consequently, states also changed the month of their elections. To reduce constant electoral competition, some states holding off-cycle elections also homogenized elections after the reform. 25Political advertising slots are specifically allocated for these purposes five months prior to federal elections (Lar- reguy, Marshall and Snyder forthcoming). 26Table A12 shows that the results are robust to defining upcoming elections by any number of months between 1 and 12.

17 sumption. While this assumption is plausible in a context where all states repeatedly hold elections, this design substantially reducing the identifying variation: because half the states in the dataset never experience an election within 5 months of an election, there is no within-state variation in the treatment for half the sample.

4.3 Upcoming elections increase news consumption and political knowledge

The results in panel A-C of Table1 demonstrate that local elections increase both the likelihood that a voter consumes any political information at all as well as the level of information consumed. Column (1) of panel A shows that an upcoming local election increases the probability that a voter listens to or watches news at all by 5 percentage points.Only consuming news before elections is likely to represent a conscious acquisition choice by voters that had previously avoided the relatively extensive news coverage also available outside election campaigns. Column (1) in panel B also reports a large increase in weekly news and political program consumption. The positive effect on the five-point scale in column (1) of panel C is also statistically significant. These findings suggest that voters with both lower and higher baseline levels of engagement consume more political information prior to statewide elections. Panel D shows that the cycle of increased information consumption prior to elections mirrors changes in political knowledge. Contrary to potential concerns about social desirability bias, column (1) demonstrates that voters facing an upcoming local election are more than a quarter of a standard deviation—or 9 percentage points—more likely to correctly answer a question testing their political knowledge.27 This increase suggests that voters actively engage by internalizing political information, a likely prerequisite for political information to influence electoral accountability. Column (2)-(8) demonstrate the robustness of such political information cycles at both the extensive and intensive margins of political news consumption. First, to address the imbalance over education, column (2) shows that the findings are qualitatively similar when including fixed effects for all five educational categories. This alters the sample because education was not measured in 2005. Second, at notable efficiency cost, column (3) reports the difference-in-differences results including state fixed effects. Although this approach effectively drops observations from states that do not experience an upcoming election in any survey (more than half the sample), the results are relatively stable and generally remain statistically significant in spite of the reduced precision in this subset of states. Third, the results do not depend upon the particular definition of the upcoming

27Interacting upcoming local elections with baseline covariates for both consumption and knowledge outcomes suggests that the same voters consuming more news also become more knowledgeable about politics.

18 Table 1: The effect of upcoming local elections on political news consumption and topical political knowledge

(1) (2) (3) (4) (5) (6) (7) (8) Panel A: Outcome: Watch and listen to news and political programs ever Upcoming local election 0.049*** 0.033* 0.006 (0.014) (0.017) (0.018) Upcoming local election 0.093*** 0.079*** (two-month) (0.015) (0.015) Months until next election -0.002*** -0.001* -0.002*** (0.001) (0.001) (0.001)

Observations 13,030 8,330 13,030 13,030 8,330 13,030 8,330 13,030 Outcome range {0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1} Outcome mean 0.87 0.86 0.87 0.87 0.86 0.87 0.86 0.87 Treatment mean 0.19 0.24 0.19 0.02 0.03 17.53 18.88 17.53 Panel B: Outcome: Watch and listen to news and political programs weekly Upcoming local election 0.082*** 0.053** 0.058* (0.022) (0.024) (0.030) Upcoming local election 0.116*** 0.095*** (two-month) (0.038) (0.030) Months until next election -0.005*** -0.005*** -0.004*** (0.001) (0.001) (0.001)

Observations 13,030 8,330 13,030 13,030 8,330 13,030 8,330 13,030 Outcome range {0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1} Outcome mean 0.63 0.63 0.63 0.63 0.63 0.63 0.63 0.63 Treatment mean 0.19 0.24 0.19 0.02 0.03 17.53 18.88 17.53 Panel C: Outcome: Watch and listen to news and political programs scale Upcoming local election 0.276*** 0.174** 0.158 (0.075) (0.079) (0.098) Upcoming local election 0.416*** 0.343*** (two-month) (0.122) (0.093) Months until next election -0.016*** -0.014*** -0.012*** (0.002) (0.003) (0.003)

Observations 13,030 8,330 13,030 13,030 8,330 13,030 8,330 13,030 Outcome range {0,1,2,3,4}{0,1,2,3,4}{0,1,2,3,4}{0,1,2,3,4}{0,1,2,3,4}{0,1,2,3,4}{0,1,2,3,4}{0,1,2,3,4} Outcome mean 2.58 2.57 2.58 2.58 2.57 2.58 2.57 2.58 Outcome standard deviation 1.47 1.49 1.47 1.47 1.49 1.47 1.49 1.47 Treatment mean 0.19 0.24 0.19 0.02 0.03 17.53 18.88 17.53 Panel D: Outcome: Topical political knowledge Upcoming local election 0.312*** 0.152*** 0.119*** (0.051) (0.036) (0.044) Upcoming local election 0.218** 0.188** (two-month) (0.102) (0.080) Months until next election -0.006*** -0.003** -0.002 (0.002) (0.001) (0.001)

Observations 17,213 12,513 17,213 17,213 12,513 17,213 12,513 17,213 Outcome range [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] Outcome mean 0.00 0.00 0.00 0.00 0.00 0.00 0.00 0.00 Outcome std. dev. 1.00 1.00 1.00 1.00 1.00 1.00 1.00 1.00 Treatment mean 0.16 0.18 0.16 0.03 0.04 18.58 19.88 18.58 Municipalities 539 386 539 539 386 539 386 539 Education ﬁxed effects XXX State ﬁxed effects XX

Notes: All specifications include survey-year fixed effects, and are estimated using OLS. The outcomes in panels A-C were not collected in the 2001 survey, and education was not collected in 2005. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01. 19 election indicator. Columns (4)-(5) instead define an upcoming local election as a survey within two months before election day. Although only 2% of observations (from 4 states) experience such an election,28 the larger point estimates provide further confidence that voters indeed consume most political information before elections. Adopting a linear approach, columns (6)-(8) similarly confirm that voters exhibit greater news consumption and political knowledge as the number of months until the next local election decreases.

5 Local violence and electoral accountability

Given that voters consume signiﬁcantly more news just before elections, signal of incumbent quality covered in the news at this time may inﬂuence voting behavior in contexts where voters possess relatively low baseline levels of political information. To test this, I exploit plausibly exogenous spikes in the occurrence of homicides—a widely-covered news event—before elections to identify the electoral effects of short-term performance indicators coinciding with voter news consumption cycles. I contrast the effect of such pre-election homicide shocks with longer-term homicide rates—likely to be more accurate signals of performance, but less frequently observed due to voter cycles in politically-relevant information consumption.

5.1 Data

To examine the electoral effects of violence in the run-up to elections I utilize two main sources of data. First, electoral returns for municipal, state, and federal elections covering Mexico’s c.67,000 electoral precincts were assembled from the Federal Electoral Institute (IFE),29 state electoral in- stitutes, and freedom of information requests. I focus primarily on municipal elections between 1999 and 2013, for which data is widely available across all states, while state and federal electoral returns are used to parse accountability channels. Since municipal elections generally occur every three years, the full dataset contains around four elections per municipality. Second, I combine the electoral data with the INEGI’s monthly municipal homicide data (described in section 3.2). The empirical analysis focuses on two measures of incumbent electoral performance: a municipal- level indicator for whether the incumbent party won the election, and the precinct-level change in the incumbent party’s vote share.30 Reﬂecting their persisting state-level power (Langston 2003),

28Since only 4 states have within-state variation, state ﬁxed effects are not added. 29IFE recently became the National Electoral Institute (INE). 30Table A13 shows similar results the incumbent vote share level as a robustness check. Given that the analysis weights by the number of registered voters in each precinct and standard errors are clustered by municipality, the precinct-level vote share estimates are almost identical to municipal-level estimates. Because some precincts are

20 53% of incumbent mayors in the sample are from the PRI; 29% are PAN and 12% are PRD. As noted above, voters generally sanction parties for the performance of their politicians in Mexico’s party-centric system.31 The average incumbent party experiences a 5.7 percentage point decline in their vote share, but still wins 54% of races. Turnout rates are typically around 60%. Municipali- ties without their own police forces, including the delegations of the Federal District, are excluded from the analysis because mayors have limited capacity to affect homicide rates.32

5.2 Identiﬁcation strategy

While the national homicide rate has changed relatively smoothly over time, this masks considerable inter-month volatility within municipalities. At the height of the War on Drugs in 2010, the monthly homicide count in Ciudad Juarez,´ Chihuahua, oscillated dramatically, e.g. from 394 in September to 477 in October before falling to 242 in November and again rising to 309 in Decem- ber. Conversely, the median municipality experienced only one homicide over a year. More generally, municipal homicides counts appear to ﬂuctuate fairly random in the short-run: the month- to-month count is almost exactly as likely to increase as decrease—both in the run-up to elections and in the middle of a municipal government’s tenure.33 To plausibly identify the electoral effects of homicides occurring when voters consume most politically-relevant news, I exploit short-term deviations from trend in the number of homicides around local elections.34 Speciﬁcally, I compare municipalities experiencing a short-term spike in the number of homicides just before a local election, relative to just after that election, to otherwise similar municipalities experiencing at least as many homicides just after the election as

missing within municipalities, a precinct-level analysis allows more municipal-election observations. 31In the 32% of cases where the incumbent won as part of a coalition formed by several parties, and given such coalitions can vary across elections, if the coalition changes I define the incumbent as the party with the largest vote share at the following election. In general, coalitions are dominated by large parties; the three main parties represent more than 90% of incumbents. Table2 shows that the results are robust to restricting attention to incumbents containing the three largest parties and single-party incumbents. 32Using the descriptions of municipal public security forces provided by the municipal governments in the 2000, 2002, 2004, 2011, and 2013 National Census of Municipal Governments (ENGM) surveys, and imputing data for missing years, I exclude municipalities without a police force or relying on state, federal, community, private, or other security forces. Given the difficulty of assigning responsibility, the few municipalities with inter-municipal and civil association-run police are excluded. Appendix A.3.1 describes the imputation procedure. Table A14 shows that the main findings are robust to including the approximately 100 municipalities excluded for lacking a police force. 33Across municipalities since 1999, the monthly homicide change was positive in 11.86% of cases and negative in 11.79% of cases. In election months, these shares are 11.90% and 11.87%. In the month preceding an election, the shares are 11.87% and 11.86%. Most changes are zero because most municipalities do not experience a homicide. This ratio is identical when conditioning on a homicide in either the last month or the current month. 34A benefit of the unavailability of the number of homicides reported by broadcast media stations is that the empirical strategy is not susceptible to differential media reporting biases. Table A6 shows that delayed homicide registration, a potential indicator of strategic registration and missing homicides, is balanced over homicide shocks.

21 before. Akin to Ferraz and Finan’s (2008) comparison of Brazilian municipalities, where federal audit reports were randomly released just before and just after municipal elections, I ensure that the comparison group captures similar municipalities (in homicide levels as well as other characteristics) by focusing on municipalities experiencing at least one homicide around the election.35 Formally, a municipality m is deﬁned as experiencing a pre-election homicide shock if, conditional on at least one homicide occurring over the four months spanning the penultimate month before an election and the second month after an election, m experiences more homicides in the two months before an election in month τ than the two months after the election:  1 if Homicides + Homicides > Homicides + Homicides  mτ−2 mτ−1 mτ mτ+1  τ+1   and ∑ Homicidesmτ0 > 0,  τ0=τ−2   Homicides + Homicides ≤ Homicides + Homicides Homicide shockmτ := 0 if mτ−2 mτ−1 mτ mτ+1 (2)  τ+1   and ∑ Homicidesmτ0 > 0.,  τ0=τ−2  τ+1  . if ∑ Homicidesmτ0 = 0. τ0=τ−2

Since most elections are held on the first Sunday of the month, this four-month window captures the final two months of the campaign and the post-election period before the winner enters office, while covering a sufficiently short span that month-to-month changes in the homicide count are plausibly random.36 On average, Figure 2a shows that a homicide shock equates to a statistically significant increase of around 5 homicides per month in shocked municipalities relative to control municipalities. After dropping the 30% of municipalities where no homicide is registered in either the two months before or after the election, Figure A1b in the Appendix maps the final sample of 1,335 mostly larger municipalities with their own police force. Of these, 906 experience at least one election with and one election without a homicide shock between 1999 and 2013. I estimate the effects of homicide shocks just prior to the election in precinct p of municipality m in election year t using regressions of the form:

Ypmt = βHomicide shockmt + ηm + µt + εpmt, (3)

35Municipalities with no homicides around local elections also differ signiﬁcantly from even municipalities experiencing only a single homicide over the 4-month window I focus on. Municipalities without a homicide are less developed, less politically competitive, and less violent. 36For the 9% of elections held on the 16th or later of a given month, I use months τ − 1 and τ for the pre-election homicide count and τ + 1 and τ + 2 for the post-election count. Table2 shows that the results are robust to dropping elections not held during the ﬁrst half of the month.

22 where Ypmt is either a municipal-level indicator for the incumbent party winning the election or the precinct-level change in the incumbent party’s vote share relative to the previous election. Although they are not required for identiﬁcation, municipality and year ﬁxed effects—respectively,

ηm and µt—are included to increase precision and ensure that the estimates do not capture time- invariant municipality characteristics of common shocks. I show below that similar results obtain without these ﬁxed effects. All observations are weighted by the number of registered voters. This strategy for isolating exogenous shocks relative to longer-run trends is preferred to a design examining changes in pre-election homicides rates across consecutive electionsThis is because it is hard to purge the correlation between short-term increases in the homicide rate and the longer- run homicide trends that I seek to differentiate pre-election shocks from. Nevertheless, Table A16 reports broadly similar results using a difference-in-differences design to examine deviations between pre-election homicide rate and the homicide rate over the entire preceding electoral cycle.

5.3 Evidence supporting the identiﬁcation strategy

The key identifying assumption is that the timing of homicides around elections is effectively random. Although month-to-month changes in homicide rates appear idiosyncratic at first glance, this does not necessarily imply that differences in homicide shocks across elections in a given municipality occurred by chance. This subsection validates the plausibility of the identifying assumption. I start by showing that pre-election homicide shocks are uncorrelated with a wide variety of observable pre-treatment covariates. First, Appendix Table A6 examines 99 time-varying and time-invariant covariates capturing demographic, socioeconomic, media coverage, and political features of each municipality.37 Only 11 differences are statistically significant at the 10% level.38 Most importantly, homicide shocks are equally distributed across political variables including the incumbent’s previous vote share, the competitiveness of the previous election, and the incumbent’s party identity, but also with respect to the number of media stations, the share that own a television or radio, and educational attainment. Second, shocked municipalities experience indistinguishable homicide levels and trends from non-shocked municipalities before elections. Figure 2a shows that the difference in monthly homicides between treated and untreated precincts is both relatively constant over the 10 months preceding the period used to define homicide shocks and never statistically significant.39 In fact, almost all the difference reflects a single observation—the extremely high homicide rate in Ciudad Juarez´

37Municipality fixed effects are excluded for the time-invariant 2010 Census variables. Table A7 shows analogous tests for precinct-level outcomes. 38The same number of significant imbalances arise if municipality and year fixed effects are excluded. 39Fewer homicides in treated municipalities would downwardly bias estimates if voters sanction greater violence.

23 in 2010. The balance tests in Table A6 also confirm that the average number of homicides in the 12, 6, and 3 months preceding the period defining the treatment do not significantly vary with homicide shocks. The balance tests further show that, for the 2011-2013 period when disaggre- gated crime reports coincide with my sample, homicide shocks are not significantly correlated with pre-election spikes in other types of major crime. Contrary to concerns about strategic reporting, a mismatch between the month in which a homicide occurred and was reported is equally rare across in shocked elections. Furthermore, I show below that a placebo shock defined 6 months prior to the election does not influence electoral outcomes, and that the results are robust to controlling for pre-election monthly homicide counts. Third, consistent with sampling variability, Figure 2b shows that the distributions of two-month homicide counts prior to the period defining a shock, just before elections, and just after elections are similar. If homicide counts were to instead reflect strategic manipulation, we might instead expect to observe a spike in the density around 0 or spikes in the tail of the distributions just before the election. However, comparing the distribution of homicides 2 months prior to the election and over prior 2-month periods, Kolmogorov-Smirnov tests fail to reject equality of distribution in each case. Appendix Figure A2 further shows—both graphically and using Kolmogorov-Smirnov tests—that these distributions do not differ by homicide shock status. I also find no evidence to support the more specific concern that DTOs alter the number of homicides around elections to signal their preferred electoral outcome (e.g. Alesina, Piccolo and Pinotti 2016), potentially by colluding with local governments. Table A6 shows that pre-election homicide shocks are not significantly correlated with the number of drug-related homicides in the prior year, for the 2006(Dec.)-2011 period when monthly data was made publicly available by the Mexican National Security System. Homicide shocks are also balanced across municipalities registering more than one drug-related homicide in any pre-election year over this period and where DTOs are present. At the precinct-level, Table A7 shows that shocks are no more likely to occur in the 5% of precincts designated by the IFE as high-risk (typically locations with high DTO activity). In addition, Table2 shows that the results are robust to removing municipalities with high levels of drug-related homicides and states with high DTO presence. Nevertheless, the types of homicide could change without affecting overall levels. Gangland killings are typically concentrated among young and uneducated men (Dell 2015), and are often committed using firearms or more gruesome methods—particularly if intended as signals. Using the International Classification of Diseases codes in INEGI’s coroner reports, Table A6 also examines the causes of death and victim characteristics associated with homicides occurring in the two months before an election. In particular, homicide shocks are balanced with respect to the share

24 Before After 10 election election 5 .2 0 .15 -5 .1 -10 Density

Difference in monthly homicides Monthly before - after -15 difference: 5.3*** Monthly before - after .05 difference: 4.2*** -20 12 11 10 9 8 7 6 5 4 3 2 1 0 -1 Months until election 0 0 5 10 15 20 25 Full sample Excluding Ciudad Juárez 2010 Average number of homicides per month

(a) Difference in the number of homicides between Months 9 and 10 before election Months 7 and 8 before election Months 5 and 6 before election Months 3 and 4 before election municipalities with and withouta pre-election Months 1 and 2 before election Months 1 and 2 after election homicide shock, by month until the election (95% (b) Distribution of homicides by relation to election conﬁdence intervals)

Figure 2: Distribution of homicides by homicide shock and over time Notes: Each bar in Figure 2a denotes the difference in the number of homicides in treated (positive shock) and control (negative shock) municipalities in the ten months prior to the period defining the homicide shock around the election. Similarly, the before-after difference is the difference between in the monthly average number of homicides over the two month before and after the election. Each estimate is from a regression akin to the main estimating equation (3). The few cases of more than 25 homicides per month are not shown in Figure 2b to facilitate graphical representation. of pre-election homicides caused by a firearm, hanging, or chemical substances. Of relatively fre- quent types of homicide, only cutting-related homicides were greater in homicide shock elections before the election. Furthermore, these homicides did not disproportionately afflict young, male, unmarried, or uneducated individuals that are most likely to be involved with organized crime in shocked municipalities. Another potential concern is that homicide counts change before elections because high-capacity governments can crack down on crime prior to elections to win votes. Although no expert on municipal politics that I interviewed believed that municipal governments crack down on local homicides in the short-term, I examine this concern more systematically. First, proxies for state capacity—including municipality size and budget, police per voter, alignment with governors or the president, and neighbor homicide shocks—are uncorrelated with homicide shocks. This suggests no differential ability to engage in such crackdowns. Second, using Osorio’s (2015) newspaper-based measures of DTOs crackdowns, Table A6 further demonstrates that homicide shocks are not significantly correlated with violent enforcement, drug-related arrests, asset seizures, drug seizures, and gun seizures in the two months before the election.

25 Finally, deﬁning homicide shocks using post-election homicides could introduce bias if election outcomes themselves affect post-election homicides counts. However, new mayors do not enter ofﬁce within two months of the election. Furthermore, Table A8 shows that neither pre-election political variables nor election outcome variables predict homicide levels in the two months after an election.40 Post-election homicides are also uncorrelated with interactions between election outcomes and background covariates. Nevertheless, as noted above, Table A16 reports similar results examining pre-election deviations from trend in the homicide count based only on pre- election data.

5.4 Pre-election homicide shocks harm municipal incumbent parties

Table2 shows that pre-election homicide shocks substantially harm the municipal incumbent party’s electoral prospects. Column (1) of panel A reports that such homicide shocks reduce the incumbent party’s probability of being re-elected by 12 percentage points. This represents a 21% reduction in a mayor’s re-election probability relative to municipalities not experiencing a pre- election homicide shock. Column (1) of panel B reports that this decline reflects a 2.2 percentage point reduction in the incumbent party’s vote share. This equates to 0.45 percentage points for each additional homicide per month relative to the baseline levels in the treatment and control group. Table A11 indicates that the decline in incumbent vote share principally reflects greater turnout for non-incumbent parties. These sharp differences are robust to various checks. First, the results are not sensitive to possible violations of the identifying assumption. Column (2) shows that the results do not depend upon including municipality and year fixed effects, which also adds 429 elections to the sample from municipalities where a homicide shock is only defined for a single election. However, the greatest identification threat reflects time-varying unobservables. To address possible concerns, column (3) of Table2 first demonstrates robustness to including 32 time-varying municipal-level covariates.41 Column (4) next includes state-year fixed effects to control for election-specific state- level shocks. Columns (5) and (6) further include incumbent-specific (for the three largest parties) and municipality-specific linear trends to ensure that the results are respectively not driven by differential trends across different types of incumbent parties or municipalities. Finally, I conduct a placebo test where a homicide shock is defined six months earlier, according to equation (3). The results in column (7) show that such pre-campaign shocks, which could be indicative of pre-trends,

40Dell(2015) similarly ﬁnds that homicide rates increased where PAN mayors were elected during the Calder on´ administration, but not during the “lame duck” quarter before such mayors entered ofﬁce. 41To preserve sample size, I the few exclude variables with greater than 95% missingness from this control set.

26 Table 2: Effects of pre-election homicide shocks on municipal incumbent electoral outcomes

Baseline No ﬁxed Controls State- Incumbent Municipality Placebo Violence Fewer than Few Non- One- Three- Four- First Main Single- spec. effects year party -speciﬁc 6 months bin 25 homicides drug DTO month month month half of party party effects trends trends earlier effects per month homicides states shock shock shock month incumbent incumbent (1) (2) (3) (4) (5) (6) (7) (8) (9) (10) (11) (12) (13) (14) (15) (16) (17) Panel A: Outcome: Incumbent party win Homicide shock -0.122*** -0.088** -0.075** -0.100*** -0.110*** -0.124** -0.129*** -0.105*** -0.122*** -0.111** -0.116*** -0.123*** -0.140** (0.039) (0.035) (0.036) (0.031) (0.040) (0.063) (0.035) (0.040) (0.039) (0.050) (0.042) (0.039) (0.057) Placebo homicide -0.017 shock (0.053) Homicide shock -0.047 (one month) (0.047) Homicide shock -0.111*** (three month) (0.042) Homicide shock -0.085** (four month) (0.041)

Observations 2,852 3,281 2,689 2,852 2,544 2,852 2,408 2,843 2,831 2,852 1,895 1,891 3,496 3,977 2,622 2,544 1,762 Unique municipalities 906 1,335 865 906 823 906 820 906 905 906 616 637 1,064 1,172 854 823 641 Outcome range {0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1} Outcome mean 0.55 0.55 0.55 0.55 0.55 0.55 0.55 0.55 0.54 0.55 0.54 0.55 0.54 0.54 0.55 0.55 0.55 Homicide shock mean 0.41 0.42 0.41 0.41 0.42 0.45 0.41 0.41 0.42 0.41 0.41 0.48 0.43 0.42 0.41 0.42 0.39 Panel B: Outcome: Change in incumbent party vote share Homicide shock -0.022*** -0.018** -0.015** -0.018*** -0.015* -0.029*** -0.027*** -0.022** -0.022*** -0.026** -0.019** -0.022*** -0.034*** (0.009) (0.007) (0.006) (0.007) (0.008) (0.011) (0.009) (0.009) (0.009) (0.010) (0.009) (0.008) (0.012) Placebo homicide -0.005 shock (0.012)

27 Homicide shock -0.015 (one month) (0.011) Homicide shock -0.024*** (three month) (0.009) Homicide shock -0.026*** (four month) (0.009)

Observations 167,116 173,115 162,774 167,116 157,639 167,116 145,511 167,116 155,267 167,116 102,126 143,840 180,302 188,067 152,539 157,639 104,220 Unique municipalities 906 1,335 895 906 823 906 820 906 905 906 616 637 1,064 1,172 854 823 641 Outcome range [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.87] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] Outcome mean -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.06 -0.05 -0.05 -0.06 -0.05 -0.05 -0.04 Outcome std. dev. 0.14 0.14 0.14 0.14 0.14 0.14 0.14 0.14 0.15 0.14 0.14 0.14 0.15 0.15 0.14 0.14 0.15 Homicide shock mean 0.41 0.42 0.41 0.41 0.42 0.47 0.41 0.41 0.42 0.41 0.41 0.48 0.43 0.42 0.41 0.42 0.39

Notes: Columns (2) includes the controls in Table A6, with the exception of variables with greater than 5% missingness. Column (3) excludes municipality and year fixed effects, and thus includes municipalities 429 municipalities where a homicide shock is only defined for one election where electoral data is available. Column (4) includes state-year fixed effects. Column (5) includes party-specific incumbent year trends. Column (6) includes municipality-specific year trends. Column (7) uses a placebo homicide shock defined six months before the election. Column (8) includes fixed effects for the total number of homicides over the four-month window in bins of size ten. Column (9) excludes municipalities averaging more than 25 homicides per month over the two months either before or after the election. Column (10) excludes municipalities that average more than one drug-related homicide a month over the 12 months before an election between 2006 and 2011. Column (11) excludes states with high-level of DTO activity (see footnote 43). Columns (12)-(14) respectively define homicide shocks over one-, three-, and four-month windows. Column (15) includes only elections that take place on or before the 15th of the month. Column (16) includes only elections where the PAN, PRD, or PRI are an incumbent. Column (17) includes only observations where the incumbent is not a coalition. All specifications are estimated using OLS, and all observations are weighted by the number of registered voters in the electoral precinct. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01. do not affect incumbent electoral performance. Second, the results do not reflect municipalities experiencing particular levels or types of homicide. By including fixed effects for the total number of homicides over the four-month window used to define homicide shocks (in 10-homicide bins), column (8) provides further evidence that the results are not driven by differences in homicide levels across shocked and non-shocked municipalities.42 Moreover, column (9) excludes the 21 municipality-elections experiencing more than 25 homicides per month before or after the election to demonstrate that the results do not simply reflect a few large municipalities with many homicides. Although homicide shocks are uncorrelated with indicators of DTO presence, to further address the concern that the results are driven by strategic political violence in areas with high drug-related criminal activity, I exclude the elections most vulnerable to strategic political violence by DTOs. Specifically, column (10) excludes municipalities that average more than one drug-related murder a month over any pre-election year between 2006 and 2011 (when such data were registered), while column (11) excludes 9 states with high DTO-related drug crime.43 In neither case do the estimates substantially change. Third, the results are not driven by particular measures of homicide shock or electoral outcome. First, columns (12)-(14) show that homicide shocks defined by one-, three-, or four-month comparisons also reduce the incumbent’s probability of winning by 5-11 percentage points and vote share by around 2 percentage points. The smaller effects associated with the one-month comparison may reflect the weaker signal imparted by shocks defined by fewer homicides. Column (15) shows that the results are robust to removing elections that occurred in the second half of the month. These elections are more challenging to classify with respect to homicides occurring before the election because they are more scattered within the month. Column (16) restricts attention to PAN, PRD, and PRI incumbents, demonstrating that the results are not driven by the few mayors from smaller parties. Consistent with a clearer assignment of responsibility, column (17) reports slightly larger effects, especially on vote share, when restricting attention to single-party incumbents. Together, these results robustly show thata temporary increase in local homicides can have substantial electoral implications for an incumbent when the spike coincides with the pre-election period when voters consume more political information.

42Bins of size 1 and 5 similarly yield signiﬁcant effects, at the cost of fully-explaining municipality-elections with a unique large number of homicides. 43Baja California, Chihuahua, Durango, Guerrero, Michoacan,´ Nuevo Leon,´ Sinaloa, Sonora, and Tamaulipas.

28 5.5 No effect of longer-run homicide rates

The political information cycles argument implies that voters are particularly likely to respond to homicides that occur just before elections. In contrast, longer-run homicide metrics may not affect voters’ responsibility attribution if, as already shown, many voters are insufﬁciently engaged at other times in the political cycle to learn about more systematic trends in homicide levels. To examine whether homicide shocks before elections indeed induce greater incumbent sanctioning than long-run homicide rates, I estimate the effects of homicides over the prior year and prior (three-year) electoral cycle on the incumbent party’s electoral prospects in a difference-in- differences framework.I thus compare changes in support for incumbent parties in municipalities that experienced large increases in their longer-run homicide rate between elections to changes in support for incumbent parties in municipalities that did not using the following speciﬁcation:

Ypmt = βAverage monthly homicide ratemt + ηm + µt + εpmt. (4)

As a robustness check, municipality-specific time trends are included to account for differential trends in incumbent support across municipalities experiencing different homicide rates. The results in Table3 indicate that long-run homicide trends have had limited impact on electoral outcomes. The point estimates in columns (1), (2), (5), and (6) of panel A show that homicides over the year before the election are not significantly correlated with either the incumbent’s probability of being re-elected or their vote share, regardless of the inclusion of municipality-specific time trends. In fact, the estimates in columns (5) imply that 5 more homicides a month over the year before an election—almost one a third of a standard deviation increase—only translates into a 0.15 percentage point decline in the municipal incumbent party’s vote share. This effect is around 15 times smaller than the five-homicide monthly average differential between shocked and non-shocked municipalities just before elections. Columns (3), (4), (7), and (8) include a quadratic term, but also find little suggestion that any effect is non-linear. Panel B similarly shows that voters do not sanction homicide rates averaged across the full electoral cycle. The evidence thus suggests that longer-run homicide trends play comparatively little role in informing electoral accountability.

5.6 Voters distinguish responsibility across levels of government

Although mayors playa role in local public security, state and federal governments are also important players. The punishment of municipal mayors could then reﬂect broader punishment of the party controlling higher ofﬁce. Conversely, if voters believe that mayors are primarily responsible

29 Table 3: Effects of longer-run municipal homicide rates on municipal incumbent electoral outcomes

Incumbent party win Change in incumbent party vote share (1) (2) (3) (4) (5) (6) (7) (8) Panel A: Effect of homicides 12 months before election Average monthly homicide rate 0.0009 -0.0031 -0.0009 -0.0005 -0.0003 -0.0006 -0.0014 -0.0023 (12 months before election) (0.0016) (0.0019) (0.0062) (0.0080) (0.0003) (0.0006) (0.0012) (0.0023) Average monthly homicide rate 0.0000 -0.0000 0.0000 0.0000 (12 months before election) squared (0.0000) (0.0000) (0.0000) (0.0000)

Observations 2,852 2,852 2,852 2,852 167,116 167,116 167,116 167,116 Unique municipalities 906 906 906 906 906 906 906 906 Outcome range {0,1}{0,1}{0,1}{0,1} [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] Outcome mean 0.55 0.55 0.55 0.55 -0.05 -0.05 -0.05 -0.05 Outcome standard deviation 0.50 0.50 0.50 0.50 0.14 0.14 0.14 0.14 Homicide rate mean 8.42 8.42 8.42 8.42 8.42 8.42 8.42 8.42 Homicide rate standard deviation 22.28 22.28 22.28 22.28 22.39 22.39 22.39 22.39

30 Municipality-speciﬁc time trends XXXX Panel B: Effect of homicides since last election Average monthly homicide rate 0.0027 -0.0028 0.0039 0.0075 -0.0002 -0.0000 -0.0004 -0.0001 (3 years before election) (0.0019) (0.0040) (0.0084) (0.0147) (0.0003) (0.0008) (0.0014) (0.0033) Average monthly homicide rate -0.0000 -0.0001 0.0000 0.0000 (3 years before election) squared (0.0000) (0.0001) (0.0000) (0.0000)

Observations 2,852 2,852 2,852 2,852 167,116 167,116 167,116 167,116 Unique municipalities 906 906 906 906 906 906 906 906 Outcome range {0,1}{0,1}{0,1}{0,1} [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] Outcome mean 0.55 0.55 0.55 0.55 -0.05 -0.05 -0.05 -0.05 Outcome standard deviation 0.50 0.50 0.50 0.50 0.14 0.14 0.14 0.14 Homicide rate mean 7.20 7.20 7.20 7.20 7.18 7.18 7.18 7.18 Homicide rate standard deviation 15.29 15.29 15.29 15.29 15.32 15.32 15.32 15.32 Municipality-speciﬁc time trends XXXX

Notes: All specifications are estimated using OLS, and include municipality and year fixed effects. All observations are weighted by the number of registered voters for the relevant electoral unit. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01. for local crime (or that their actions are only weakly correlated with co-partisans at higher levels), they may update less about national parties following local homicide shocks. I next disentangle these chains of accountability and responsibility assignment. If voters believe that the mayor is responsible for local crime because they control the local police, pre-election homicide shocks should only be punished in municipalities with their own police force. To test this, I add municipalities (and delegations in the Federal District) without their own police force to the sample. Consistent with voters recognizing that elevated homicides rates may be beyond the control of municipal mayors without local police forces, panel A of Table 4 shows that homicide shocks only significantly harm the electoral prospects of incumbent parties commanding a local police force. Columns (2) and (4) address the concern that the effect attributed to police forces reflects the lack of sanctioning in smaller and less developed municipalities by controlling for the interaction of a homicide shock with previous incumbent party vote share and the average monthly homicide rate over the last year.44 Contrary to the naive perspective on voting behavior, this finding suggests that voters are not indiscriminately punishing adverse events. Nevertheless, if the parties of municipal mayors, state deputies, state Governors, or the Pres- ident are correlated, the substantial electoral penalties documented at the municipal level could instead reflect punishment of higher political actors. The results in columns (1)-(3) of Table5 suggest that, if anything, homicide shocks increase the municipal vote share of the state deputy’s, governor’s, and president’s parties’, and thus provide no support for punishment at higher levels of government spilling over to municipal elections.45 Alternatively, voters could restrict punishment for state and federal politicians in their corresponding races. However, columns (4) and (5) indicate that a homicide shock reduces neither the vote share of state nor federal deputies in concurrent state and federal elections. Although there is no evidence to suggest that state and federal incumbent parties are held responsible for homicide shocks by voters, the punishment of the local party could also spill up to the national level. However, when municipal and higher-level elections are held concurrently, columns (6) and (7) of Table5 show that the state and federal deputy vote shares of the municipal incumbent’s party are not significantly affected by a homicide shock. Table A17 further shows that voters do not differentially punish particular parties for homicide shocks.

44Table A20 provides mixed evidence that voters account for homicide shocks affecting neighboring municipalities. 45Consistent with Table A17 in the Appendix, the positive effect at the federal level reﬂects increased support for Calderon’s´ PAN government.

31 Table 4: Electoral effects of homicide shocks, by presence of municipal police force Incumbent Change in incumbent party win party vote share (1) (2) (3) (4) Homicide shock -0.122*** -0.130*** -0.023*** -0.024*** (0.037) (0.038) (0.008) (0.007) No municipal police force 0.002 0.023 0.006 -0.005 (0.099) (0.098) (0.016) (0.014) Homicide shock 0.236* 0.234** 0.065*** 0.050** × No municipal police force (0.124) (0.116) (0.023) (0.022)

Observations 3,398 3,360 195,119 195,119 Unique municipalities 1,026 1,019 1,026 1,026 Outcome range {0,1}{0,1} [-0.96,0.89] [-0.96,0.89] Outcome mean 0.58 0.58 -0.04 -0.04 Homicide shock mean 0.41 0.41 0.41 0.41 Interaction mean 0.14 0.14 0.14 0.14 Test: Homicide shock + Homicide shock × 0.32 0.33 0.05 0.21 No municipal police force = 0 (p value) Interactive controls XX Notes: All speciﬁcations include municipal and year ﬁxed effects, weight by the number of registered voters, and are estimated using OLS. The interactive controls are lagged incumbent party vote share and average monthly homicides over the last year (both standardized, and × Homicide shock). Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01.

6 The amplifying effect of local media

The individual- and aggregate-level findings suggest that the electoral sanctioning of local homicides principally reflects increased voter news consumption before elections. This implication of political information cycles relies on voters having access to locally-based media likely to report on local events (e.g. Snyder and Stromberg¨ 2010). Given that media sources may bias their reporting of news in different ways (e.g. Besley and Prat 2006; Gentzkow and Shapiro 2006; Mullainathan and Shleifer 2005) and market segmentation may mean that not all types of station reach all voters (Barabas and Jerit 2009; Prat and Stromberg¨ 2005), the likelihood that voters consume relevant local news—and thus hold municipal incumbents to account—is likely to increase with the number of local media outlets voters have access to. To examine the extent to which sanctioning of homicide shocks reflects such media coverage, I combine pre-election homicide shocks with plausibly exogenous precinct-level variation in media signal coverage to estimate the effect of an additional local radio or television station likely to report on such shocks.

32 Table 5: Electoral effects of homicide shocks, by level of government

Change in municipal vote share of... Change in Change in Change in Change in ...state ...state ...President’s state deputy federal state vote of federal vote of district Governor’s party incumbent incumbent municipal municipal party party vote share vote share incumbent incumbent (1) (2) (3) (4) (5) (6) (7) Homicide shock 0.001 0.029** 0.032* -0.004 -0.005 0.008 -0.017 (0.009) (0.015) (0.018) (0.009) (0.015) (0.016) (0.017)

Observations 143,226 135,849 167,116 135,153 52,661 128,109 62,450 Unique municipalites 892 845 906 895 391 875 413 Outcome mean 0.00 0.03 0.03 -0.04 -0.05 0.45 0.38 Outcome std. dev. 0.13 0.17 0.24 0.14 0.13 0.17 0.13 Homicide shock mean 0.42 0.42 0.41 0.41 0.42 0.42 0.43

Notes: All speciﬁcations include municipal and year ﬁxed effects, weight by the number of registered voters, and are estimated using OLS. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01.

6.1 Data

As part of Mexico’s major media reform in 2007 (see Larreguy, Marshall and Snyder forthcoming; Serra 2012), the IFE required that all radio and television stations in the country submit detailed coverage and technological data. This included the location and power of their antennae and a map detailing their commercial quality coverage—the level of coverage that media stations may base advertising sales on and which the IFE deemed relevant for minimizing cross-state advertising spillovers. The signal inside the commercial quality coverage area is very strong, and should cover virtually all households. However, signal quality declines quickly as the distance from the commercial quality coverage boundary increases.46 Figure3 maps the commercial quality coverage of each type of media station. While FM radio, and especially television, stations have limited and primarily urban coverage, AM radio stations can travel considerable distances—particularly when aided by stretches of sea water with high electrical ground conductivity. Virtually all of the population is covered by at least one media station, but the number of outlets—both emitting from within a municipality and without—providing commercial quality signals to any given electoral precinct varies considerably. Following Larreguy, Marshall and Snyder(2018), I deﬁne an electoral precinct as covered by a given media station if at least 20% of voters fall within the commercial coverage boundary.47

46The IFE deﬁnes the boundary of the coverage area using a 60 dBµ threshold for signal strength. According to the U.S.-based National Communications and Information Administration, this “60 dBµ level is recognized as the area in which a reliable signal can be received using an ordinary radio receiver and antenna.” This is the threshold commonly used to determine a radio station’s audience and sell advertising space commercially in theUS. 47The INEGI provides detailed Census population counts in 2010, for both rural localities and urban blocks. This

33 (a) AM radio stations (b) FM radio stations (c) Television stations

Figure 3: Media station commercial quality signal coverage areas

6.2 Identiﬁcation strategy

To estimate the electoral effects of an additional media station covering local homicides, I leverage geographic variation in coverage on the intensive margin (see also Larreguy, Marshall and Snyder 2018; Spenkuch and Toniatti 2016). I compare neighboring electoral precincts within the same municipality that differ in the total number of local AM, FM, and television stations—defined as outlets whose antennae are located within the electoral precinct’s municipality and that provide local content48—by which they are covered.49 Since signal quality rapidly, but not entirely, declines across the commercial quality boundary, this strategy identifies an “intent to treat” effect of increasing the probability of exposure to an additional local media station.50 Figure4 illustrates the identification strategy graphically in case of a local television station, using the example of electoral precincts 1571 and 1583 from the same municipality in Oaxaca. The identifying assumption is that these neighboring precincts differ only because precinct 1583 receives a commercial quality signal from a local television station that does not cover precinct 1571. More generally, for each electoral precinct, I identify the set of neighboring precincts from within the same municipality that differ in the number of local media stations that they are covered by. Each such grouping n is defined by a single “treated” precinct and the set of “control” neighboring precincts that receive different local media exposure. Focusing on municipalities included in the homicide shock sample produced 2,689 neighboring groups, containing an average of 2.3

data is used to identify the proportion of voters within a precinct covered by a commercial quality signal. 48Local content excludes television stations solely retransmitting Televisa and TV Azteca national broadcasts. 49Although data does not exist to adjust for news consumption “non-compliance,” any effect would be larger among compliers that only receive news because they were exposed to an additional commercial quality local signal. 50Exposure to commercial quality coverage does not constitute a geographic regression discontinuity design because the treatment is not binary (some neighbors differ by more one media station) and where neighbors differ by more than one media station it is not clear how to coherently deﬁne the running variable.

34 Figure 4: Identification strategy example Notes: Both precincts are located in the municipality of Villa de Tututepec de Melchor Ocampo in the state of Oaxaca. Precinct 1583 is covered by the local television emitting from within the municipality, but precinct 1571 is not. comparison units per election. The average precinct in this sample is covered by 6.3, 8.9, and 3.2 local AM, FM, and television stations respectively.The total number of local media stations covering a precinct ranges from 0 to 40.51 There are good reasons to believe that, among neighboring electoral precincts, local media coverage at the commercial quality boundary is exogenous. First, neighboring precincts often differ in coverage because of physical characteristics such as water, geographic contours, and large objects that aid or impede ground conductivity (in the case of AM radio) and “line of sight” radio waves (in the case of FM radio and television) between an antenna and precincts at the coverage boundary (Larreguy, Marshall and Snyder 2018; Olken 2009). Second, given that media stations lack the technology to differentiate media markets at fine-grained levels,52 and voters who locate according to the availability of local media are unlikely to choose to live close to a coverage boundary (pre- ferring a location guaranteeing high-quality coverage), it is unlikely that coverage reflects strategic sorting by either media stations or voters around coverage boundaries. Finally, I restrict attention to neighboring precincts with an area of less than 2km2. This removes larger precincts where media outlets could more plausibly target their signals, and prevents stark comparisons between urban and suburban, or suburban and rural, precincts that may respond differently to homicide shocks for other reasons. The final sample is shown in Figure A1c.

51Given that data from the Secretariat of Communications and Transportation show that the number of media stations has barely changed since 2003, I continue to pool the years 1999 to 2013. 52The IFE data show that the power of signal transmitters are fairly discrete. The power output in watts for AM, FM, and television stations is almost exclusively round thousands that are divisible by ﬁve.

35 Combining this within-neighbor variation in local media coverage with the homicide shocks leveraged above,I use the following speciﬁcation to estimate the interaction between pre-election homicide spikes and local media coverage:

Ypnmt = β1Homicide shockmt + β2Local mediap +β3 Homicide shockmt × Local mediap + ζn + µt + εpnmt, (5)

53 where ζn is a fixed effect for each set of neighboring precincts. To weight comparisons within each neighbor-year set equally, each “treated” precinct is weighted by electorate size and “control” precincts are weighted by electorate size divided by the number of controls per neighbor-year set. To assess the claim that differences in local media coverage between neighboring precincts reflect plausibly exogenous topological features, I use equation (5) to examine balance across demographic, socioeconomic, homicide, and political municipal and precinct characteristics.54 Table A9 shows that only 8 of these 92 variables are significantly correlated with the number of local media stations at the 10% level. In particular, there are no significant differences in key indicators of rural-urban geography (such as precinct area, electorate size, or distance to the municipality head), the number of non-local media stations, homicide indicators, or previous electoral outcomes.I show below that the results are robust to controlling interactively for the significant imbalances.

6.3 Local media increase punishment of homicide shocks

Column (2) of Table6 shows that access to local media stations plays a significant role in supporting the electoral sanctioning of homicide shocks in this sample of predominantly urban precincts.55 Indicating that local media are necessary for Mexican voters to punish the incumbent party for pre-election homicides, the null lower-order effect of a homicide shock shows that pre-election homicide spikes do not affect electoral outcomes in precincts without access to local media. How- ever, the significant negative interaction coefficient implies that each additional local media station reduces the vote share of incumbents experiencing a pre-election homicide shock by 0.2 percentage points. For more than eight local media stations (79% of the sample), Figure5 shows that the overall effect of a homicide shock is to substantially reduce the municipal incumbent party’s vote share.56 The positive coefficient on the lower-order local media term suggests that voters may

53Since I use within-municipality neighbors, neighbor fixed effects incorporate municipality fixed effects. 54Table A10 shows that homicide shocks remain well-balanced across pre-treatment variables in this subsample. 55Column (1) shows that the effect of homicide shocks is larger in the local media subsample. 56Since the identification strategy relies on within-neighbor variation, this represents a linear extrapolation of the average marginal effect.

36 ihe peicswt nae f1mo es rmr eeosrsrcin 5mo eso oarea no or less or permitted. (5km area restrictions precinct generous maximum more considering or the to less) on robust or restriction) are 1km of results area the an that with local show (precincts a (10)-(12) tighter whether Columns define to precinct. used a cutoff covers 20% the station to media sensitive not are estimates the that demonstrate first sample. smaller results this The in estimates precinct. similar “treated” provide group’s approach neighboring (2009)-type Olken each further or this of to, of station nearer meters media 50 local than average more column no the are results, from, that the precincts driving comparison to not sample generally—is the restricts more (6) thus municipalities antennae—and within sig- radio precincts from with of distance variables that location the 8 ensure the the to that Third, of demonstrates media. version similarly local standardized over (5) imbalances for they column nificant interactively because controlling Second, shocks to homicide robust general. to are in more results media respond to simply access not greater do precincts that media possess show local to precinct to a access covering greater outlets media with non-local of number the for controls tively additional 3%. each approximately by that share indicates vote (3) party’s column incumbent in natural the alters used The station stations election. media media the local local before of shock number homicide the a of experience logarithm not do that incumbents reward also iue5 lcoa feto oiiesok odtoa ntenme flclmdastations media local of number the on conditional shock, homicide a of effect Electoral 5: Figure oevr fterslside eetlclmdacvrn oiiesok htocrjust occur that shocks homicide covering media local reflect indeed results the if Moreover, (7)-(9) Columns choices. design particular on depend not do results the that shows also 6 Table interac- (4) column First, identification. to threats potential various to robust are findings The lt h itiuino h oa ei aibei h sample. the in variable media local the of distribution the plots Notes h rydniyaoethe above density gray The 6. Table of (1) column from estimates the using Calculated :

Marginal effect of a homicide shock -.15 -.1 -.05 0 .05 0 9%cndneinterval) conﬁdence (95% 10 Number oflocalmediastations 37 20 30 40 x axis Table 6: Effect of homicide shocks on precinct-level change in incumbent party vote share, moderated by access to local and non-local media

Outcome: Change in incumbent party vote share No local Baseline Logarithmic Interactive Interactive Average 10% 50% 100% media local transformation non-local imbalanced control media precinct precinct precinct media media control controls within 50m coverage coverage coverage (1) (2) (3) (4) (5) (6) (7) (8) (9) Homicide shock -0.0563*** -0.0148 0.0220 -0.0114 -0.0143 -0.0143 -0.0222 -0.0095 -0.0009 (0.0153) (0.0249) (0.0364) (0.0300) (0.0234) (0.0240) (0.0248) (0.0249) (0.0176) Local media 0.0017* 0.0017* 0.0016* -0.0001 0.0013 0.0007 0.0017** (0.0009) (0.0009) (0.0009) (0.0011) (0.0008) (0.0012) (0.0009) Homicide shock × Local media -0.0023** -0.0024** -0.0024** -0.0023** -0.0020** -0.0023** -0.0027*** (0.0010) (0.0010) (0.0009) (0.0010) (0.0009) (0.0009) (0.0007) Local media (log) 0.0249*** (0.0089) Homicide shock × Local media (log) -0.0291** (0.0114) Non-local media -0.0002 (0.0009) Homicide shock × Non-local media -0.0001 (0.0008)

Observations 29,736 29,736 29,736 29,736 29,736 11,606 29,533 33,056 51,288 Unique municipalities 118 118 118 118 118 115 116 123 198 Outcome range [-0.63,0.50] [-0.63,0.50] [-0.63,0.50] [-0.63,0.50] [-0.63,0.50] [-0.63,0.50] [-0.63,0.50] [-0.63,0.50] [-0.64,0.61] Outcome mean -0.04 -0.04 -0.04 -0.04 -0.04 -0.04 -0.04 -0.04 -0.05 Outcome standard deviation 0.13 0.13 0.13 0.13 0.13 0.13 0.13 0.13 0.13 Homicide shock mean 0.40 0.40 0.40 0.40 0.40 0.40 0.41 0.39 0.42 Media measure media mean 18.69 18.69 18.69 18.69 18.76 19.93 20.49 18.49 Media measure standard deviation 10.30 10.30 10.30 10.30 10.32 11.14 10.84 11.25 1km area 5km area No area Longer-run Non-local AM ad FM TV ad restriction restriction restriction homicides media incumbent incumbent incumbent share share share (10) (11) (12) (13) (14) (15) (16) (17) Homicide shock -0.0169 -0.0101 0.0126 -0.0095 -0.0054 -0.0174 -0.0080 (0.0299) (0.0210) (0.0142) (0.0184) (0.0826) (0.0521) (0.0441) Local media 0.0016 0.0021*** 0.0012* 0.0010 (0.0010) (0.0007) (0.0007) (0.0009) Homicide shock × Local media -0.0023* -0.0026*** -0.0027*** (0.0012) (0.0009) (0.0008) Average monthly homicide rate 0.0024 (3 years before election) (0.0018) Average monthly homicide rate (3 years -0.0001 before election) × Local media (0.0001) Non-local media 0.0000 (0.0004) Homicide shock × Non-local media -0.0005 (0.0004) Incumbent ad share -0.1320 -0.0168 -0.0843 (0.2326) (0.1341) (0.1130) Homicide shock × Incumbent ad share -0.0637 -0.0168 -0.0527 (0.3018) (0.1923) (0.1594)

Observations 25,297 35,323 101,713 29,736 92,596 33,643 33,643 33,643 Unique municipalities 91 139 375 118 383 379 379 379 Outcome range [-0.63,0.47] [-0.63,0.53] [-0.90,0.89] [-0.63,0.50] [-0.75,0.73] [-0.77,0.87] [-0.77,0.87] [-0.77,0.87] Outcome mean -0.04 -0.04 -0.05 -0.04 -0.05 -0.07 -0.07 -0.07 Outcome standard deviation 0.13 0.13 0.15 0.13 0.14 0.13 0.13 0.13 Homicide shock mean 0.39 0.41 0.45 15.31 0.46 0.43 0.43 0.43 Media measure media mean 19.69 17.90 13.23 18.69 8.89 0.27 0.27 0.26 Media measure standard deviation 9.99 10.48 10.78 10.30 9.56 0.06 0.08 0.08

Notes: All speciﬁcations include neighbor group and year ﬁxed effects, and are estimated using OLS. All observations are weighted by the number of registered voters divided by the number of comparison units within each neighbor group. The (standardized) interactive controls in column (4) are omitted to save space. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01.

38 before elections, then content that media outlets have weak incentives to report should not alter vote choices. In particular, news that is not recent or not relevant to a media outlet’s audience is likely to be broadcast less. In line with these expectations, columns (13) and (14) find no significant interaction between longer-run homicide levels and access to local media or between pre-election homicide shocks and non-local media. Nevertheless, voters could still be influenced by content that also references homicide shocks, beyond the news and political programming of local media outlets themselves. Mexico’s election campaign ads are the most likely source, although they mostly contain national content (Larreguy, Marshall and Snyder forthcoming). However, columns (15)-(17) report no evidence that the share of broadcast media ads allocated to the party of the municipal incumbent moderates the effects of homicide shocks. These falsification tests suggest that electoral sanctioning occurs where media outlets are likely to report on local homicides at the time when voters consume most news, and thus emphasize the importance for voting behavior of the intersection between the consumption and supply of politically-relevant news.

7 Mechanisms and interpretation

The preceding analysis showed that voters consume most political information just before elections, and are responsive to homicides that occur at this time, but only when covered by local media stations likely to report such news. This section explores the mechanisms driving these political information cycles. I ﬁnd that voters update their beliefs in a Bayesian manner, before showing that political information cycles are more likely driven by changes in voter demand for news than changes in media coverage around elections.

7.1 Voter belief updating reﬂects political information cycles

By examining voter beliefs directly, I test whether the preceding results reflect political information cycles. If news consumption reflects political information cycles, voters will principally update their beliefs—potentially both about the incumbent’s performance and the importance of addressing security concerns—in response to events occurring just before elections. However, the observed aggregate voting behavior is also consistent with several alternative explanations. First, pre-election homicide spikes could induce emotional electoral responses that do not rely on voters updating—whether in a naive or sophisticated manner—about incumbent quality (Achen and Bartels 2017; Healy, Malhotra and Mo 2010). Second, cycles of information consumption may not be driving the results if voters’ beliefs only reflect recent events (Zaller 1992). In this case, pre-election homicides would drive election outcomes because voter beliefs did not

39 permanently incorporate news consumed earlier. Third, voters may only respond to pre-election homicide shocks because incumbents have time to win back disgruntled voters when homicide spikes occur earlier in their terms (Brollo 2009). In contrast with the political information cycles argument that voters are unlikely to react to events during periods where they consume little news, these alternative explanations imply that voters should also update in the short-term outside of electoral campaigns as well (i.e. while homicides remain recent or before incumbents respond). To distinguish between these accounts, I use the ENCUP surveys to examine how voter concerns about public security and confidence in elected officials vary with homicide shocks during and outside local election campaigns.57 I define an indicator for respondents citing crime and insecurity, drug trafficking, violence, or vandalism as the most important problem for their community to solve.58 I also create an indicator of low confidence in the municipal mayor, defined by respondents ranking their confidence at 5 or below on a scale from 0 to 10 (for 2012) or expressing no, or almost no, confidence (in 2001, when a ten-point scale was not provided).59 The results in Table7 extend equation (1) by interacting upcoming local elections with pre-survey homicide shocks (defined analogously to pre-election homicide shocks) and longer-term monthly homicide rates that are unlikely to be reported.60 The plausible exogeneity of both upcoming local elections and pre-survey homicide shocks credibly identifies the lower-order and interaction effects.61 The results in Table7 demonstrate that homicide shocks just before an election increase fears regarding public security and reduce confidence in the mayor. The insignificant effects of the lower-order homicide shock terms in columns (1) and (2) of panel A, combined with the large positive interactions, imply that homicide shocks only increase concerns about security among voters in municipalities experiencing an upcoming local election. Relative to the sample mean, a homicide shock increases security concerns by almost 50% during an election campaign. Columns (1) and (2) of panel B report similar results for confidence in the mayor, showing that only pre- election homicide shocks induce voters to reduce such confidence, by up to one third of the sample mean. For both outcomes, the lower-order upcoming local election coefficients suggest that while

57The Federal District, where policing is not administered at the delegation-level, is excluded. 58Along with all other political concerns, I include as zeroes respondents that do not cite a problem. 59The cutoff on the 0-10 scale was chosen to broadly match the distribution of responses in 2001. However, the results do not depend upon the choice of cutoff. Vote intentions were not elicited in any survey wave. 60Since the day of the survey varies, but homicide data is monthly, a homicide in the month of the survey could occur after the survey was carried out. I address this by deﬁning a homicide shock as occurring if, relative to the two months after the survey was conducted, there were more homicides either in the two months preceding the survey month or the preceding month and survey month itself. In 2005, when day of month is available, I use the two preceding months for the 15th or earlier, and the preceding month and survey month for the 16th or later. 61Supporting this design, Tables A3 and A4 show that short-run homicide shocks, and their interaction with upcoming local elections, are not systematically correlated with individual-level and municipal covariates.

40 Table 7: Heterogeneous effects of upcoming local elections on concern for public security and conﬁdence in the mayor, by short-run and long-run municipal homicide measures Homicide measure: Pre-survey Homicides per Homicides per homicide shock month last year month last 3 years (1) (2) (3) (4) (5) (6) Panel A: Outcome: Public insecurity the major problem in the community Upcoming local election 0.040** -0.028 0.039** 0.002 0.039** 0.003 (0.020) (0.022) (0.016) (0.016) (0.016) (0.016) Homicide measure 0.002 -0.005 0.011*** 0.008*** 0.011*** 0.008*** (0.014) (0.010) (0.002) (0.001) (0.002) (0.001) Upcoming local election 0.060** 0.071*** 0.001 0.001 0.001 0.001 × Homicide measure (0.029) (0.025) (0.003) (0.002) (0.003) (0.002)

Observations 10,632 10,632 13,428 13,428 13,428 13,428 Clusters 302 302 423 423 423 423 Outcome range {0,1}{0,1}{0,1}{0,1}{0,1}{0,1} Outcome mean 0.14 0.14 0.12 0.12 0.12 0.12 Local election mean 0.22 0.22 0.20 0.20 0.20 0.20 Homicide measure mean 0.47 0.47 3.27 3.27 3.35 3.35 Survey year without data 2012 2012 2012 2012 2012 2012 Panel B: Outcome: Low conﬁdence in the municipal mayor Upcoming local election -0.029 0.169 -0.006 0.091 -0.006 0.093 (0.041) (0.109) (0.035) (0.056) (0.038) (0.058) Homicide measure -0.049** -0.024 0.001 0.001 0.001*** 0.001** (0.024) (0.020) (0.001) (0.001) (0.000) (0.000) Upcoming local election 0.114** 0.077 -0.001 0.010 -0.002 0.012 × Homicide measure (0.047) (0.145) (0.009) (0.011) (0.015) (0.021)

Observations 6,453 6,453 7,764 7,764 7,764 7,764 Clusters 293 293 384 384 384 384 Outcome range {0,1}{0,1}{0,1}{0,1}{0,1}{0,1} Outcome mean 0.35 0.35 0.35 0.35 0.35 0.35 Local election mean 0.02 0.02 0.03 0.03 0.03 0.03 Homicide measure mean 0.42 0.42 6.48 6.48 7.08 7.08 Survey years without data 2003, 2005 2003, 2005 2003, 2005 2003, 2005 2003, 2005 2003, 2005 State fixed effects XXX Notes: All specifications include survey year fixed effects, and are estimated using OLS. The number of observations in columns (1) and (2) is lower because voters in municipalities failing to experience any homicide over the two months either side of the survey were dropped. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01.

41 voters may become somewhat more positive when a homicide shock does not occur, any positive changes are far smaller than the negative changes associated with homicide shocks. Furthermore, and reinforcing voters’ perception that municipal governments are responsible for local homicides (implied by the precinct-level results in Table5), Appendix Table A18 shows that pre-election homicide shocks do not cause voters to lose confidence in the president or their state governor. Given that some voters do consume news outside of election campaigns, it is perhaps surprising that homicide shocks do not affect beliefs at other times as well. This could be because changes in beliefs and voting behavior are concentrated among the voters that shift from consuming very little news outside election campaigns to more regular consumption before elections. More fre- quent consumers of news—who are, on average, significantly more educated—may be harder to influence because their greater news consumption engenders more precise prior beliefs that are harder to shift. Table A21 supports this claim: voters without higher education update their beliefs about public security being a major problem and reduce their confidence in the mayor more in response to pre-election homicide shocks, while the effect of local media covering such shocks on incumbent vote share is lower in precincts with below-median levels of higher education. It remains possible that voters are actually responding to longer-run homicide rates. The lower- order terms unsurprisingly show that public security is a greater concern in more violent municipalities. However, the placebo-like tests in columns (3)-(6), which interact upcoming local elections with longer-term homicide measures, do not support this possibility. These results suggest that voter responses are not simply emotional, but entail belief updating. Moreover, highlighting the importance of information consumption cycles, the insignificant effects of a homicide shock outside local election campaigns imply that voters do not consume information and react similarly outside of election campaigns, just without durably updating their beliefs. The results are instead consistent with voters only internalizing events likely to have been reported in the news before elections. Nevertheless, although beliefs change, this analysis cannot establish the extent to which belief updating is sophisticated or actually influences voting behavior.

7.2 Prior beliefs moderate voter responses to homicide shocks

To better assess whether voting behavior reflects sophisticated belief updating, I consider more nuanced responses to homicide shocks. If voters respond in a Bayesian manner, their reaction to homicide shocks will interact with their prior beliefs about incumbent and challenger parties. I test for such learning by examining whether homicide shocks before the previous election—a plausible proxy for voters’ prior beliefs about the competence of the current incumbent party (if still in office) or challenger parties (if a different party was previously in office), given voters’

42 ocrsadsgaigmdl rdcigta aeinvtr ilsnto ihhmcd rates. homicide high sanction career will the voters to Bayesian credibility that greater predicting lend models thus signaling that and and manner, suggesting concerns sophisticated results a survey in the beliefs reinforce their election findings update previous These voters the at sanctioning. shock voter homicide no a experienced over and presided party different a where a bar, the from fourth between incumbent the is previous sanctioning—and contrast substantial at starkest entail office the shocks However, in homicide was cases—where shock. two a incumbent first experience current not the did where but bar, election third previous the the the for if are than effects large magnitude These under also in shocks. is larger election homicide shock pre-election somewhat previous consecutive homicide for the office a in of before was effect party shock incumbent negative same a the Similarly, such party. the experience incumbent before not different shock a did homicide which a and experiencing whether election municipalities in and current voters election party. among previous incumbent greatest the previous is the before sanctioning from shock differs homicide party a incumbent current of the occurrence the with varies manner. share nuanced a such in respond to unlikely are voters Zallerian naive homicide Conversely, pre-election shocks. of effects electoral precinct-level the consumption—moderate news cyclical 62 soshwteefc fahmcd hc ntecag nteicmetprysvote party’s incumbent the in change the on shock homicide a of effect the how shows 6 Figure rvossoki nidctrfrahmcd hc curn eoetepeiu election. previous the before occurring shock homicide a for indicator an is shock Previous Notes iue6 h feto oiiesoko h hnei nubn at oesae by share, vote party incumbent in change the on shock homicide a of effect The 6: Figure A19. Table in provided are estimates regression associated The aeicmeti nidctrfrtecreticmetprywnigtepeiu election. previous the winning party incumbent current the for indicator an is incumbent Same : rvoshmcd hcsadicmetiett 9%cndneintervals) confidence (95% identity incumbent and shocks homicide previous

Marginal effect of homicide shock Different incumbent,

no previousshock -.1 -.05 0 .05 .1 Same incumbent, previous shock 43 no previousshock Same incumbent, Different incumbent, previous shock 62 h rtbrsosthat shows bar ﬁrst The 7.3 Media coverage of violent crime is not more common during local election campaigns

So far, this article has treated political information cycles as an equilibrium outcome. However, from both a theoretical and policy perspective, it is important to understand whether these cycles reflect changes in voter demand for politically-relevant news and/or changes in the media’s supply of such news around elections. The increased political news consumption at the extensive margin documented in Table1 suggests that tuning in for the news is a conscious choice, given that radio and television schedules do not change around elections. However, for the many voters increasing consumption along the intensive margin, it is hard to separate increased voter interest in following news before elections from news providers broadcasting more politically-relevant news before elections. For news relating to local homicides, a first step in separating these effects is to examine changes in coverage around elections. In the absence of comprehensive broadcast media tran- scripts, I use newspaper data from Osorio(2015). He uses machine-learning techniques to collate reports relating to drug violence from 105 government agencies and national and local newspapers between 2000 and 2010. The resulting report counts capture the frequency of coverage, but not its tone. Broadcast media coverage is likely to be similar, given that newspapers serve as an important information source for broadcast media outlets in developing contexts (Keefer and Khemani 2016). In a nationwide survey of local newspapers and radio stations, 64% report sourcing news from other local media outlets (Larreguy, Lucas and Marshall 2016). To test whether reporting of violent events increases before elections in the municipalities used for the main analysis,I examine whether the correlation between the occurrence and reporting of violent events increases within the five months before local elections using the following difference-in-differences specification:

Reportsmt = β1Homicidesmt + β2Upcoming local electionmt +β3 Upcoming local electionmt × Homicidesmt + ηm + µt + εmt, (6) where Reportsmt is a month-year municipal-level count of the number of violent events (including homicides as well as shootings, kidnappings, torture etc.) between DTOs reported for that month,63 and µm and µt are municipality and month-year ﬁxed effects. The results in Table8 show a strong positive correlation between homicides and violent events,

63The outcome was aggregated up from Osorio’s (2015) weekly count. Similar results obtain when using reports of violent enforcement, arrests, drug seizures, asset seizures, and gun seizures.

44 Table 8: Correlation between monthly municipal homicide counts and government agency and newspaper reports on violence between gangs, by upcoming local elections Number of inter-DTO violence reports per month-year (1) (2) (3) (4) (5) Homicides per month 0.236*** 0.225*** 0.237*** 0.237*** 0.226*** (0.026) (0.024) (0.026) (0.026) (0.024) Upcoming local election 0.005 (0.018) Homicides per month -0.005 -0.006 -0.004 × Upcoming local election (0.017) (0.017) (0.014)

Observations 117,780 117,780 117,780 117,780 117,780 Clusters 906 906 906 906 906 Outcome range [0,102] [0,102] [0,102] [0,102] [0,102] Outcome mean 0.28 0.28 0.28 0.28 0.28 Outcome std. dev. 2.12 2.12 2.12 2.12 2.12 Homicides per month mean 0.93 0.93 0.93 0.93 0.93 Homicides per month std. dev. 5.24 5.24 5.24 5.24 5.24 Upcoming local election mean 0.15 0.15 0.15 0.15 0.15 Additional ﬁxed effects State × Election × Election × state month-year month-year × month-year

Notes: All specifications include municipality and year-month fixed effects, and are estimated using OLS. Stan- dard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01. but that such coverage is not significantly greater before elections. Column (1) first demonstrates that for each homicide that occurs in a municipality, the number of violent events reported increases by 0.24. Since not all newspapers are studied and reports only pertain to drug-related violence, this estimate likely understates the propensity of newspapers to report homicides. Turning to differential coverage around elections, column (3) shows that reporting is not significantly greater in the five months preceding local elections. This is broadly consistent with surveys of media outlets in 2017, which indicate that while politics in general is covered more before elections, only 18% (5%) of outlets report on public security issues more (less) than usual before elections (Larreguy, Lucas and Marshall 2016). Both sets of results are precisely estimated, and are robust to including state-month-year fixed effects (and their interaction with upcoming local elections). These findings indicate that media coverage of homicides is not sensitive to the electoral cycle, and thus suggest that the sanctioning of pre-election homicides is more likely driven by increased voter demand for politically-relevant news before elections than changes in the supply of such news.

45 8 Conclusion

This study demonstrates the importance of the timing of voter news consumption for understanding how voters hold governments to account. Leveraging survey and electoral returns data, and identification strategies isolating three central and complementary components of the political information cycles argument, I show that voters indeed consume more politically-relevant news before elections, and that pre-election homicide shocks substantially reduce support for the municipal incumbent party among voters exposed to local media likely to report on such events. Conversely, there is little evidence that long-run performance homicide indicators affect electoral outcomes. Although this paper’s evidence draws from Mexico, its findings are likely to apply more broadly to contexts where voters do not regularly consume news outside of election campaigns and to issues that are similarly salient to voters. Political knowledge levels are low in many democracies, especially in the developing world. In the U.S., major news stories preceding elections seem to frequently and substantially influence election results. Moreover, macroeconomic outcomes and corruption revelations may evoke similarly strong responses from voters, given the ease which media outlets can explain—and potentially dramatize (Baum 2002)—its link to politician performance. Consequently, understanding the origins and further substantiating mechanisms underpinning political information cycles demands further research. First, this article did not attempt to separate between the factors—such as consumption benefits, social pressure, or civic duty—that induce voters to demand more news before elections. Second, although the frequency of newspaper coverage of homicides does not change during election campaigns, it is important to establish the extent to which such stability extends to the tone of coverage and to other more explicitly political news stories. Third, this study addressed the issue of media bias by simply focusing on access to an average local media outlet. However, it may be important to move beyond access to examine the extent to which coverage is politically slanted (Gentzkow and Shapiro 2010; Gentzkow et al. 2015), and the agenda is strategically determined (Durante and Zhuravskaya forthcoming; Eisensee and Stromberg¨ 2007). Finally, exactly what voters infer from pre-election homicides warrants deeper examination. While I observe updating consistent with Bayesian information processing, additional data is required to distinguish whether voters learn from homicide spikes occurring or from responses in their aftermath. Another open question regards the normative implications of political information cycles. Whether voting on the basis of noisy pre-election performance signals, which add noise to the selection process, reduces voter welfare depends on the factors that would have determined vote choices

46 otherwise. Although exogenous pre-election homicide shocks might cause voters to downweight signals that are more informative about desirable politician characteristics, in contexts like Mexico it is also possible that clientelistic relationships are broken down, which could increase welfare if clientelism perpetuates the rule of low-quality incumbents. Nevertheless, the possibility that information reduces the efficiency of election mechanisms chimes with other theoretical results showing that it cannot be assumed that greater political information is necessarily welfare en- hancing (Ashworth and Bueno de Mesquita 2014; Ashworth, Bueno de Mesquita and Friedenberg forthcoming). Ultimately, whether homicide shocks—and other captivating news stories—result in the election of worse politicians and lower performance are empirical questions of significant interest policy-makers designing informational interventions. Regardless of the welfare implications, it is clear that political parties, interest groups, and NGOs should strategically target incumbent performance information toward the least informed voters around elections—when voters consume political news. While such groups may use information to support their goals, it is essential that purely informative news should relate to horizons beyond proximate security or economic shocks, and thus provide the longer-term indicators that voters profess to value (Healy and Lenz 2014). Although NGO-supported interventions have at- tempted to achieve this, often by delivering leaflets or newspapers (e.g. Banerjee et al. 2011; Chong et al. 2015; Dunning et al. forthcoming), broadcast media appears to be the most effective tool for dissemination (Ferraz and Finan 2008; Larreguy, Marshall and Snyder 2018). Consequently, a key challenge is encouraging political actors and media stations to overcome sensationalist and political biases in favor of longer-term performance indicators.

47 References

Achen, Christopher H. and Larry M. Bartels. 2017. Democracy for realists: Why elections do not produce responsive government. Princeton University Press.

Adena, Maja, Ruben Enikolopov, Maria Petrova, Veronica Santarosa and Ekaterina Zhuravskaya. 2015. “Radio and the Rise of the Nazis in Prewar Germany.” Quarterly Journal of Economics 130(4):1885–1939.

Alesina, Alberto, Salvatore Piccolo and Paolo Pinotti. 2016. “Organized Crime, Violence, and Politics.” Working paper.

Anderson, Christopher J. 2007. “The end of economic voting? Contingency dilemmas and the limits of democratic accountability.” Annual Review Political Science 10:271–296.

Arias, Eric, Horacio A. Larreguy, John Marshall and Pablo Querub´ın. 2018. “Priors rule: When do malfeasance revelations help and hurt incumbent parties?” Working paper.

Arnold, R. Douglas and Nicholas Carnes. 2012. “Holding mayors accountable: New York’s exec- utives from Koch to Bloomberg.” American Journal of Political Science 56(4):949–963.

Ashworth, Scott. 2005. “Reputational dynamics and political careers.” Journal of Law, Economics, and Organization 21(2):441–466.

Ashworth, Scott. 2012. “Electoral accountability: recent theoretical and empirical work.” Annual Review of Political Science 15:183–201.

Ashworth, Scott and Ethan Bueno de Mesquita. 2014. “Is Voter Competence Good for Voters? Information, Rationality, and Democratic Performance.” American Political Science Review 108(3):565–587.

Ashworth, Scott, Ethan Bueno de Mesquita and Amanda Friedenberg. 2017. “Accountability and information in elections.” American Economic Journal: Microeconomics 9(2):95–138.

Ashworth, Scott, Ethan Bueno de Mesquita and Amanda Friedenberg. forthcoming. “Learning About Voter Rationality.” American Journal of Political Science .

Baker, Andy, Barry Ames and Lucio R. Renno. 2006. “Social context and campaign volatility in new democracies: networks and neighborhoods in Brazil’s 2002 Elections.” American Journal of Political Science 50(2):382–399.

48 Banerjee, Abhijit V., Selvan Kumar, Rohini Pande and Felix Su. 2011. “Do Informed Voters Make Better Choices? Experimental Evidence from Urban India.” Working paper.

Barabas, Jason and Jennifer Jerit. 2009. “Estimating the Causal Effects of Media Coverage on Policy-Speciﬁc Knowledge.” American Journal of Political Science 53(1):73–89.

Barabas, Jason, Jennifer Jerit, William Pollock and Carlisle Rainey. 2014. “The Question (s) of Political Knowledge.” American Political Science Review 108(4):840–855.

Bateson, Regina. 2012. “Crime victimization and political participation.” American Political Sci- ence Review 106(3):570–587.

Baum, Matthew A. 2002. “Sex, lies, and war: How soft news brings foreign policy to the inattentive public.” American Political Science Review 96(1):91–109.

Berrebi, Claude and Esteban F. Klor. 2006. “On terrorism and electoral outcomes theory and evidence from the Israeli-Palestinian conﬂict.” Journal of Conﬂict Resolution 50(6):899–925.

Besley, Timothy and Andrea Prat. 2006. “Handcuffs for the grabbing hand? Media capture and government accountability.” American Economic Review 96(3):720–736.

Besley, Timothy and Robin Burgess. 2002. “The political economy of government responsiveness: Theory and evidence from India.” Quarterly Journal of Economics 117(4):1415–1451.

Blais, Andre.´ 2000. To vote or not to vote? The merits and limits of rational choice theory. University of Pittsburgh Pre.

Blanco, Luisa R. 2013. “The impact of crime on trust in institutions in Mexico.” European Journal of Political Economy 32:38–55.

Bobonis, Gustavo J., Luis R. Camara Fuertes and Rainer Schwabe. 2013. “Monitoring Corruptible Politicians.” Working paper.

Brender, Adi and Allan Drazen. 2005. “Political budget cycles in new versus established democracies.” Journal of Monetary Economics 52(7):1271–1295.

Brollo, Fernanda. 2009. “Who Is Punishing Corrupt Politicians—Voters or the Central Govern- ment? Evidence from the Brazilian Anti-Corruption Program.” Working paper.

49 Castaneda˜ Sabido, Fernando. 2011. “Investigacion´ sobre la percepcion´ ciudadana acerca de la transparencia, rendicion´ de cuentas y ﬁscalizacin en el uso de los recursos publicos´ en Mexico.”´ Reporte para la Auditor´ıa Superior de la Federacion´ .

Chang, Eric C.C., Miriam A. Golden and Seth J. Hill. 2010. “Legislative malfeasance and political accountability.” World Politics 62(2):177–220.

Chiang, Chun-Fang and Brian Knight. 2011. “Media bias and inﬂuence: Evidence from newspaper endorsements.” Review of Economic Studies 78(3):795–820.

Chong, Alberto, Ana De La O, Dean Karlan and Leonard Wantchekon. 2015. “Does Corruption Information Inspire the Fight or Quash the Hope? A Field Experiment in Mexico on Voter Turnout, Choice and Party Identiﬁcation.” Journal of Politics 77(1):55–71.

Cole, Shawn, Andrew Healy and Eric Werker. 2012. “Do voters demand responsive governments? Evidence from Indian disaster relief.” Journal of Development Economics 97(2):167–181.

Corbacho, Ana, Julia Philipp and Mauricio Ruiz-Vega. 2015. “Crime and erosion of trust: Evi- dence for Latin America.” World Development 70:400–415.

Cornelius, Wayne A. 1996. Mexican politics in transition: The breakdown of a one-party-dominant regime. La Jolla: Center for US-Mexican Studies, University of California, San Diego.

Da Silveira, Bernardo S. and Joao˜ M.P. De Mello. 2011. “Campaign advertising and election outcomes: Quasi-natural experiment evidence from gubernatorial elections in Brazil.” Review of Economic Studies 78(2):590–612. de Figueiredo, Miguel F.P., F. Daniel Hidalgo and Yuri Kasahara. 2013. “When Do Voters Punish Corrupt Politicians? Experimental Evidence from Brazil.” Working paper.

Degan, Arianna. 2006. “Policy Positions, Information Acquisition and Turnout.” Scandinavian Journal of Economics 108(4):669–682.

Dell, Melissa. 2015. “Trafﬁcking Networks and the Mexican Drug War.” American Economic Review 105(6):1738–1779.

DellaVigna, Stefano and Ethan Kaplan. 2007. “The Fox News effect: Media bias and voting.” Quarterly Journal of Economics 122(3):1187–1234.

50 DellaVigna, Stefano, Ruben Enikolopov, Vera Mironova, Maria Petrova and Ekaterina Zhu- ravskaya. 2014. “Cross-border media and nationalism: Evidence from Serbian radio in Croatia.” American Economic Journal: Applied Economics 6(3):103–32.

Delli Carpini, Michael X. and Scott Keeter. 1996. What Americans Know about Politics and Why It Matters.

Diaz-Cayeros, Alberto, Jose´ Antonio Gonzalez´ and Fernando Rojas. 2006. Mexico’s Decentraliza- tion at a Crossroads. In Federal and Economic Reform: International Perspectives, ed. Jessica S. Wallack and T. N. Srinivasan. Cambridge University Press pp. 364—406.

Downs, Anthony. 1957. An Economic Theory of Democracy. Addison Wesley.

Dunning, Thad, Guy Grossman, Macartan Humphreys, Susan Hyde and Craig McIntosh. forthcoming. Metaketa I: The Limits of Electoral Accountability. Cambridge University Press.

Durante, Ruben and Ekaterina Zhuravskaya. forthcoming. “Attack When the World Is Not Watch- ing? U.S. News and the Israeli-Palestinian Conﬂict.” Journal of Political Economy .

Durante, Ruben and Emilio Gutierrez. 2015. “Fighting crime with a little help from my friends: Party afﬁliation, inter-jurisdictional cooperation and crime in Mexico.” Working paper.

Durante, Ruben, Paolo Pinotti and Andrea Tesei. 2017. “The political legacy of entertainment TV.”.

Eifert, Benn, Edward Miguel and Daniel N. Posner. 2010. “Political Competition and Ethnic Identiﬁcation in Africa.” American Journal of Political Science 54(2):494–510.

Eisensee, Thomas and David Stromberg.¨ 2007. “News droughts, news ﬂoods, and US disaster relief.” Quarterly Journal of Economics pp. 693–728.

Enikolopov, Ruben, Maria Petrova and Ekaterina Zhuravskaya. 2011. “Media and political persuasion: Evidence from Russia.” American Economic Review 101(7):3253–3285.

Farnsworth, Stephen J. and S. Robert Lichter. 2011. The Nightly News Nightmare: Media Coverage of US Presidential Elections, 1988-2008. Rowman and Littleﬁeld.

Faye, Michael and Paul Niehaus. 2012. “Political aid cycles.” American Economic Review 102(7):3516–30.

51 Fearon, James D. 1999. Electoral Accountability and the Control of Politicians: Selecting Good Types versus Sanctioning Poor Performance. In Democracy, Accountability, and Representation, ed. Adam Przeworski, Susan Stokes and Bernard Manin. Cambridge University Press.

Feddersen, Timothy and Alvaro Sandroni. 2006. “Ethical voters and costly information acquisition.” Quarterly Journal of Political Science 1(3):287–311.

Ferraz, Claudio and Frederico Finan. 2008. “Exposing Corrupt Politicians: The Effects of Brazil’s Publicly Released Audits on Electoral Outcomes.” Quarterly Journal of Economics 123(2):703– 745.

Fowler, Anthony and Andrew B. Hall. forthcoming. “Do shark attacks inﬂuence presidential elections? Reassessing a prominent ﬁnding on voter competence.” Journal of Politics .

Fowler, Anthony and B. Pablo Montagnes. 2015. “College football, elections, and false- positive results in observational research.” Proceedings of the National Academy of Sciences 112(45):13800–13804.

Fox, Jonathan. 1994. “The difﬁcult transition from clientelism to citizenship: Lessons from Mex- ico.” World Politics 46(2).

Gentzkow, Matthew and Jesse M. Shapiro. 2006. “Media bias and reputation.” Journal of Political Economy 114(2):280–316.

Gentzkow, Matthew and Jesse M. Shapiro. 2010. “What drives media slant? Evidence from US daily newspapers.” Econometrica 78(1):35–71.

Gentzkow, Matthew, Nathan Petek, Jesse M. Shapiro and Michael Sinkinson. 2015. “Do newspapers serve the state? Incumbent party inﬂuence on the US press, 1869–1928.” Journal of the European Economic Association 13(1):29–61.

Greene, Kenneth F. 2007. Why Dominant Parties Lose: Mexico’s Democratization in Comparative Perspective. Cambridge University Press.

Greene, Kenneth F. 2011. “Campaign Persuasion and Nascent Partisanship in Mexico’s New Democracy.” American Journal of Political Science 55(2):398–416.

Hallin, Daniel. 2000. Media, political power, and democratization in Mexico. In De-Westernizing Media Studies, ed. James Currant and Myung-Jin Park. London: Routledge pp. 97–110.

52 Hamilton, James. 2004. All the news that’s ﬁt to sell: How the market transforms information into news. Princeton University Press.

Healy, Andrew and Gabriel S. Lenz. 2014. “Substituting the End for the Whole: Why Vot- ers Respond Primarily to the Election-Year Economy.” American Journal of Political Science 58(1):31–47.

Healy, Andrew J., Neil Malhotra and Cecilia Hyunjung Mo. 2010. “Irrelevant events affect voters’ evaluations of government performance.” Proceedings of the National Academy of Sciences 107(29):12804–12809.

Healy, Andrew and Neil Malhotra. 2013. “Retrospective Voting Reconsidered.” Annual Review of Political Science 16:285–306.

Heinle, Kimberly, Octavio Rodr´ıguez Ferreira and David A. Shirk. 2014. “Drug Violence in Mex- ico: Data and Analysis Through 2013.” Justice in Mexico Project Special Report.

Hirano, Shigeo, Gabriel S. Lenz, Maksim Pinkovskiy and James M. Snyder, Jr. 2015. “Voter Learning in State Primary Elections.” American Journal of Political Science 59(1):91–108.

Holmstrom,¨ Bengt et al. 1999. “Managerial Incentive Problems: A Dynamic Perspective.” Review of Economic Studies 66(1):169–182.

Humphreys, Macartan and Jeremy Weinstein. 2012. “Policing Politicians: Citizen Empowerment and Political Accountability in Uganda Preliminary Analysis.” Working paper.

Ibope/AGB Mexico.´ 2009. “Audiencias y Medios en Mexico.”.´

Keefer, Philip and Stuti Khemani. 2014. “Mass media and public education: The effects of access to community radio in Benin.” Journal of Development Economics 57:57–72.

Keefer, Philip and Stuti Khemani. 2016. “The Government Response to Informed Citizens: New Evidence on Media Access and the Distribution of Public Health Beneﬁts in Africa.” World Bank Economic Review 30(2):233–267.

Keefer, Phillip. 2007. Seeing and Believing: Political Obstacles to Better Service Delivery. In The Politics of Service Delivery in Democracies: Better Access for the Poor, ed. Shantayanan Devarajan and Ingrid Widlund. Stockholm: Expert Group on Development Issues pp. 42–55.

53 Kendall, Chad, Tommaso Nannicini and Francesco Trebbi. 2015. “How do voters respond to information? Evidence from a randomized campaign.” American Economic Review 105(1):322– 53.

Krosnick, Jon A. and Donald R. Kinder. 1990. “Altering the foundations of support for the president through priming.” American Political Science Review 84(2):497–512.

Langston, Joy. 2003. “Rising from the ashes? Reorganizing and unifying the PRI’s state party organizations after electoral defeat.” Comparative Political Studies 36(3):293–318.

Larcinese, Valentino. 2005. “Electoral Competition and Redistribution with Rationally Informed Voters.” BE Journal of Economic Analysis and Policy 4(1):1–28.

Larreguy, Horacio A., Christopher Lucas and John Marshall. 2016. “When do media stations support political accountability? A ﬁeld experiment in Mexico.” AEA RCT Registry 0001186.

Larreguy, Horacio A., John Marshall and James M. Snyder, Jr. 2018. “Publicizing malfeasance: How local media facilitates electoral sanctioning of Mayors in Mexico.” Working Paper.

Larreguy, Horacio A., John Marshall and James M. Snyder, Jr. forthcoming. “Leveling the play- ing ﬁeld: How campaign advertising can help non-dominant parties.” Journal of the European Economic Association .

Lawson, Chappell H. 2002. Building the fourth estate: Democratization and the rise of a free press in Mexico. University of California Press.

Lawson, Chappell and James A. McCann. 2005. “Television News, Mexico’s 2000 Elections and Media Effects in Emerging Democracies.” British Journal of Political Science 35(1):1–30.

Ley, Sandra. 2014. “Citizens in Fear: Participation and Voting Behavior in the Midst of Violence.” Dissertation.

Magaloni, Beatriz. 2006. Voting for Autocracy: Hegemonic Party Survival and its Demise in Mexico. New York: Cambridge University Press.

Marshall, John. forthcoming. “Signaling sophistication: How social expectations can increase political information acquisition.” Journal of Politics .

Martin, Gregory J and Ali Yurukoglu. 2017. “Bias in Cable News: Real Effects and Polarization.” American Economic Review 107(9):2565–2599.

54 Maskin, Eric and Jean Tirole. 2004. “The Politician and the Judge: Accountability in Government.” American Economic Review 94(4):1034–1054.

McCann, James A. and Chappell H. Lawson. 2003. “An Electorate Adrift? Public Opinion and the Quality of Democracy in Mexico.” Latin American Research Review 38(3):60–81.

Mexico´ Evalua.´ 2012. “Seguridad y Justicia Penal en los estados.” Report.

Michelitch, Kristin and Stephen Utych. 2018. “Electoral Cycle Fluctuations in Partisanship: Global Evidence from Eighty-Six Countries.” Journal of Politics 80(2):000–000.

Mullainathan, Sendhil and Andrei Shleifer. 2005. “The Market for News.” American Economic Review 95(4):1031–1053.

Olken, Benjamin A. 2009. “Do television and radio destroy social capital? Evidence from Indone- sian villages.” American Economic Journal: Applied Economics 1(4):1–33.

Ortoleva, Pietro and Erik Snowberg. 2015. “Overconﬁdence in Political Behavior.” American Economic Review 105(2):504–535.

Osorio, Javier. 2015. “The Contagion of Drug Violence: Spatiotemporal Dynamics of the Mexican War on Drugs.” Journal of Conﬂict Resolution 59(8):1403–1432.

Pande, Rohini. 2011. “Can informed voters enforce better governance? Experiments in low- income democracies.” Annual Review of Economics 3(1):215–237.

Prat, Andrea and David Stromberg.¨ 2005. “Commercial Television and Voter Information.”. CEPR Discussion Paper No. 4989.

Prior, Markus. 2007. Post-broadcast democracy: How media choice increases inequality in political involvement and polarizes elections. Cambridge University Press.

Reames, Benjamin. 2003. “Police forces in Mexico: A proﬁle.” Center for US-Mexican Studies.

Remmer, Karen L. 1991. “The political impact of economic crisis in Latin America in the 1980s.” American Political Science Review 85(3):777–800.

Roberts, Kenneth M. and Erik Wibbels. 1999. “Party systems and electoral volatility in Latin America: a test of economic, institutional, and structural explanations.” American Political Sci- ence Review 93(3):575–590.

55 Rogoff, Kenneth. 1990. “Equilibrium Political Budget Cycles.” American Economic Review 80(1):21–36.

Sabet, Daniel. 2010. Police Reform in Mexico: Advances and Persistent Obstacles. In Shared Responsibility: U.S.-Mexico Policy Options for Confronting Organized Crime, ed. Eric L. Olson, David A. Shirk and Andrew Selee. Woodrow Wilson International Center for Scholars Mexico Institute.

Semetko, Holli A. and Patti M. Valkenburg. 2000. “Framing European politics: A content analysis of press and television news.” Journal of Communication 50(2):93–109.

Serra, Gilles. 2012. “The Risk of Partyarchy and Democratic Backsliding in Mexico.” Taiwan Journal of Democracy 8(1):93–118.

Snyder, Jr, James M. and David Stromberg.¨ 2010. “Press Coverage and Political Accountability.” Journal of Political Economy 118(2):355–408.

Spenkuch, Jorg L. and David Toniatti. 2016. “Political Advertising and Election Outcomes.” Work- ing Paper.

Trelles, Alejandro and Miguel Carreras. 2012. “Bullets and votes: Violence and electoral participation in Mexico.” Journal of Politics in Latin America 4(2):89–123.

Vivanco, Edgar F., Jorge Olarte, Alberto D´ıaz-Cayeros and Beatriz Magaloni. 2015. Drugs, Bullets, and Ballots: The Impact of Violence on the 2012 Presidential Election. In Mexico’s Evolving Democracy: A Comparative Study of the 2012 Elections, ed. Jorge I. Dom´ınguez, Kenneth F. Greene, Chappell H. Lawson and Alejandro Moreno. Johns Hopkins University Press pp. 153– 181.

Wolfers, Justin. 2007. “Are Voters Rational? Evidence from Gubernatorial Elections.” Working paper.

Yanagizawa-Drott, David. 2014. “Propaganda and conﬂict: Evidence from the Rwandan geno- cide.” Quarterly Journal of Economics 129(4):1947–1994.

Zaller, John. 1992. The Nature and Origins of Mass Opinion. Cambridge University Press.

56 A Appendix Contents

A.1 Random shocks and electoral accountability with Bayesian voters...... A2 A.1.1 A career concerns model...... A2 A.1.2 An incumbent signaling model...... A5 A.2 Months and years of municipal elections...... A7 A.3 Data description...... A9 A.3.1 ENCUP survey data...... A9 A.3.2 Precinct and municipal homicide and electoral data...... A11 A.3.3 Precinct local media coverage data...... A12 A.4 Map of municipalities included in different samples...... A12 A.5 Additional analyses...... A12 A.5.1 Assessing the identiﬁcation assumptions...... A12 A.5.2 Effects on turnout...... A14 A.5.3 Additional robustness checks for the aggregate electoral results...... A22 A.5.4 Additional robustness checks for the aggregate electoral results...... A22 A.5.5 Electoral effects of drug-related homicides...... A22 A.5.6 Difference-in-differences approach to identifying the effects of pre-election homicides...... A29 A.5.7 Differential effects of homicide shocks across parties...... A30 A.5.8 Belief updating about presidents and state governors...... A33 A.5.9 Differential updating across elections...... A33 A.5.10 Learning from the experiences of neighboring municipalities...... A33 A.5.11 Less-educated voters respond most to pre-election homicide shocks.... A35

A1 A.1 Random shocks and electoral accountability with Bayesian voters

Bayesian voters will generally update from credible signals of incumbent competence or alignment with voters’ interests. For example, voters may use long-run economic performance or crime rates to infer incumbent type, on the basis that incumbent policy choices and implementation quality reﬂect underlying competence of alignment with voters’ interests. However, voters may also update from exogenous shocks, like the pre-election homicide shocks studied in the main paper. This section presents two simple models that rationalize why voters may alter their beliefs and voting behavior in response to shock beyond the incumbent’s control.

A.1.1 A career concerns model

Consider a career concerns model where an incumbent party seeks re-election in a given municipality. For simplicity, there are two electoral terms τ ∈ {1,2}, each containing T discrete periods during which a noisy signal of the incumbent’s underlying competence θ is observed—in this ap- plication, the number of homicides that occurred in the municipality during period t. The terms are split by an election, where the signal helps a unit mass of voters to decide whether to re-elect incumbent I or instead elect challenger C. The incumbent seeks to retain ofﬁce. For each term in ofﬁce, I receives “ego” rents R > 0.

Each incumbent has a ﬁxed level of competence, which is drawn from θI ∼ N (θˆ,1/hθ ), where the realization is known neither to I nor the representative voter.64 At the beginning of each term,

I can also exert costly effort aτ ≥ 0 to reduce the homicide rate, in an attempt to convince voters that they are sufﬁciently competent to merit re-election. In this context, aτ could involve allocating more resources to policing, selecting a competent chief of police with few ties to organized crime, or requiring municipal police to work with police forces at higher levels of government. The cost 0 00 of incumbent effort is c(aτ ), where c (·) > 0, c (·), and c(0) = 0. Incumbents are forward-looking and risk-neutral; they maximize p(aτ )R − c(aτ ), where p(aτ ) is the (endogenously-determined) probability of re-election. Following Holmstrom¨ et al.’s (1999) simple model, the public signal of incumbent competence— the number of homicides in the municipality in period t of term τ—is given by:

Htτ = b − θI − aτ + et, (A1) where et ∼ N (0,1/he) is a period-speciﬁc normally-distributed shock, and b > 0 is a constant

64Signaling models, like the one considered below, instead assume that the incumbent’s type is only known to the incumbent (e.g. Rogoff 1990).

A2 baseline homicide level. This shock is independent of incumbent competence and across periods, and its distribution is common knowledge. The homicide count is thus greater for less competent incumbents and incumbents that work less hard, but also reﬂects idiosyncratic factors beyond the incumbent’s control. Finally, voters elect their preferred party for the second term, based on the sum of the party’s competence and their “ideological” bias. All voters value competence equally, either directly to maintain security, or to address other issues that the ability to reduce homicides may be corre-

lated with. In addition, the ideological bias δi of voter toward Iis realized after aτ is selected, 1 1 and is uniformly-distributed such that δi ∼ U (b − 2ψ ,b + 2ψ ) with mean bias B ∈ R. Voter i compares I to challenger C, who is a random draw from the same pool as incumbents, such that

θC ∼ N (θˆ,1/hθ ). Their vote choice is vi ∈ {I,C}. The game’s timing can be summarized as:

1. Nature draw incumbent competence θI and challenger competence θC from N (θˆ,1/hθ ). This is unknown to all politicians and voters.

2. At the beginning of τ = 1, the incumbent selects a1.

3. Each voter observes T independent signals, Ht1, and their ideological bias δi is realized.

4. Each voter decides whether to re-elect the incumbent or not, vi ∈ {I,C}. The party with the majority of votes wins.

5. At the beginning of τ = 2, the incumbent (election winner) selects a2.

∗ Working backwards, any incumbent party in the second term (τ = 2) exerts effort a2 = 0, given 65 that they lack re-election incentives. Voter i votes for I (i.e. vi = I) when E[θI|H11,...,HT1,aˆ1] + δi ≥ E[θC], where aˆ1 is the voter’s conjecture about incumbent effort that needs to be ﬁltered out. Upon observing the homicide count in each period, voters’ posterior belief about incumbent competence is normally distributed with expectation:

E[θI|H11,...,HT1,aˆ1] = λ (b − H1 − aˆ1) + (1 − λ )θˆ, (A2)

The −1 T where λ := is the weight attached to the mean observed signal Hτ := T ∑ Htτ . Re- hθ +The t=1 arranging, voter i then votes to re-elect the incumbent if the number of homicides observed is

65This reﬂects the simplifying two-period assumption, although the results generalize to inﬁnitely-repeated games.

A3 δi ˆ sufﬁciently low: H1 ≤ λ + b − θ − aˆ1. Aggregating across voters yields the incumbent party’s vote share:

1 V = + B + λψ(b − H − θˆ − aˆ ) (A3) I 2 1 1

Intuitively, the incumbent’s vote share reflects average ideological biases and voter inferences about incumbent competence—the only thing that matters in the second term where there are no re- election incentives to work hard—based on the number of homicides (after filtering out incumbent effort). At the beginning of the first term, the incumbent selects their effort to reduce the number of homicides in anticipation of this voting rule. Given the ex ante re-election probability (i.e. before the number of homicides is observed), the incumbent thus solves:

" B !# aˆ1 − a1 − ψλ max 1 − Φ R − c(a1), (A4) a1≥0 h

q where h := 1 + T and Φ(·) is the Normal cumulative distribution function. In equilibrium, vot- hθ he ∗ ers’ expectations of effort are correct (i.e. aˆ1 = a1), implying that effort (in an interior equilibrium) is:66

B φ − hψλ R = c0(a∗), (A5) h 1

where φ(·) is the Normal probability distribution function. As previous career concern models have shown, effort is thus increasing in rewards (R), the relative responsiveness of voters to signals

of competence (ψ), and the precision of the signal (λ or he). The preceding analysis generates the following empirical predictions:

B ˆ ∗ Proposition 1. The incumbent is re-elected if H1 ≤ ψλ + b − θ + a1, and receives vote share 1 ˆ ∗ VI = 2 + B + ψλ (b − H1 − θ − a1). Conditional on the signal, incumbent electoral prospects decrease in H1.

Proof : follows straightforwardly from the preceding analysis. The result that incumbents overseeing more homicides are, on average, less likely to be re- elected reﬂects two sources of variation in homicide counts. First, as intended by voters, the sanctioning of high homicide counts in part captures cases where the incumbent is relatively less 66As in Ashworth(2005), the second-order condition holds for B ≤ c00(0) 1 + T p πe . hθ he 2

A4 competence (i.e. θI < θˆ). Second, because voters cannot fully solve the signal extraction problem, even rational voters willingly in part sanction the incumbent for a high average idiosyncratic

shock (e1). In contrast, because voters anticipate incumbent efforts to convince them that they are competent, such efforts are both inefﬁcient and ineffective in equilibrium. While voters respond to homicides induced by both incumbent competence and chance, these responses are moderated differently by the number of signals, T. When T is large, the idiosyncratic

shocks average out (i.e. limT→∞ e1 → 0), and thus voters extract a clear signal of competence, ∂λ which also causes the weight attached to the signal to also increase (i.e. ∂T > 0). When T is small, voters still update from, and sanction on the basis of, the observed number of homicides, but place relatively less weight on the less precise signal in casting their ballot. Consequently, variation in

homicides due to et only signiﬁcantly inﬂuences voters that consume a small number of signals (i.e. low T). In contrast, voters that consume many signals (i.e. high T) are able to achieve their

goal of sanctioning principally on the basis of variation in homicides due to θI. This logic makes clear how political information cycles can influence electoral accountability in a career concerns model. To the extent that such cycles induce voters to primarily consume news just before the election, voters will rely on a small number of signals. Since random shocks will often not average out with small T, voters with relatively imprecise prior beliefs will rationally sanction incumbents for the pre-election homicide shocks examined empirically in the main paper. If votes instead receive many signals, homicide shocks—which are shown to be uncorrelated with proxies for incumbent competence—should not influence voting behavior. In this case, longer-term homicide rates (i.e. the sum of many signals) would heavily influence vote choice.

A.1.2 An incumbent signaling model

I next develop a simple signaling model where the incumbent party responds to an exogenous homicide shock and voters update their beliefs based on their observation of this response. The model demonstrates that where politicians are generally low-quality, circumstances that allow competence politicians to reveal their type will reduce the incumbent’s vote share on average. This model contrasts with Ashworth, Bueno de Mesquita and Friedenberg(forthcoming), who gener- ate similar results in a (non-signaling) selection model where random shocks amplify or mute the role of unobserved incumbent competence in the performance outcomes voters use to evaluate incumbents, but incumbents do not act in response to shocks.67 Consider an election campaign where a unit mass of voters individually decide whether to vote

67Ashworth, Bueno de Mesquita and Friedenberg(2017) show that such insights would generalize to a career concerns-type model where politicians do not know their types.

A5 to retain an incumbent party I or vote for a challenger party C. The competence θ ∈ {θ,θ} of both I and C is only known to the party themselves, where parties are assumed to be unitary actors and θ > θ > 0. From the perspective of voters, Pr(θ) = q is the common prior belief that any politician is the more competent type (θ). Each voter has a net “ideological” bias bi ∈ R toward I (which is unknown to parties), with the distribution of shocks given by F and expectation E[bi] = b. Voters vote expressively for their preferred candidate, by maximizing the weighted sum of the politician’s expected competence and their idiosyncratic bias; i.e. they vote for the incumbent iff

E[θI|·]+ωbi ≥ E[θC|·], where ω > 0 is a common relative weight attached to the ideological bias. Voters learn about the incumbent’s competence if, with probability p ∈ (0,1), a homicide shock occurs just before the election. In particular, if a homicide shock occurs, I chooses (continuous) action a ≥ 0 to mitigate the security concern at cost a/θ, in order to maximize the difference between their vote share and their costs. For example, a could involve speaking to reporters on the radio or television in an effort to calm voter concerns about the homicide spike, proposing policies that the party would implement address security concerns, or convincing voters that the government was not responsible for the violence. For simplicity, if no homicide shock occurs, I cannot credibly signal their type to vote. When no homicide shock occurs (state N), the expected competence of both parties is θˆ = N qθ + (1 − q)θ. A voter i thus votes for I if bi ≥ 0, and I’s vote share is then VI = 1 − F(0). When a homicide shock does occur (state S), the incumbent chooses a to maximize their vote share, given the inferences voters draw from their choice of a. In any pooling equilibrium, in which a(θ) = a(θ), voters will not update and thus behave identically to the case where no homicide shock occurs. In a separately equilibrium, however, voters can learn about I’s competence. Apply- ing the Cho-Kreps intuitive criterion, a θ incumbent will always select a∗(θ) = 0 in a separating equilibrium. A θ incumbent will select a > 0 provided that the following individual rationality and incentive compatibility constraints are satisﬁed:

θˆ − θ a 1 − F − ≥ 1 − F(0), (A6) ω θ θˆ − θ a 1 − F ≥ 1 − F(0) − , (A7) ω θ

where the ﬁrst inequality ensures that θ types prefer to separate than pool, and the second inequality ensures that θ types ﬁnd it too costly to exert the level of a required to mimic θ types. The

A6 incentive constraint will bind in the separating equilibrium, implying that:

θˆ − θ a∗(θ) = θ F − F(0) , (A8) ω

∗ h θˆ−θ i subject to the rationality constraint holding, such that a (θ) ≤ θ F(0) − F ω . The space ˆ F(0)−F θ−θ in which separating equilibria exist is thus deﬁned by θ ≥ − ω . In such an equilib- θ θˆ−θ F(0)−F ω I θˆ−θ rium, the more competent incumbent’s vote share is VS (θ) = 1−F ω and the less competent I θˆ−θ incumbent’s vote share is VS (θ) = 1 − F ω . In municipalities where a separating equilibrium would exist if a homicide shock occurred, the incumbent party’s expected vote share declines when:

q(θ−θ) F ω − F(0) E[V I] − E[V I ] < 0 ⇐⇒ q < . (A9) S N q(θ−θ) q(θ−θ)−(θ−θ) F ω − F ω

This condition clearly shows that the homicides reducing the incumbent party’s electoral prospects depends on the distribution of ideological biases. In particular, homicide shocks reduce the incumbent party’s vote share when a large fraction of voters slightly favor the incumbent (relative q(θ−θ) to those slightly favoring the challenger) when no shock occurs (i.e. F ω − F(0) is large). This is because the electoral effect of better-than-expected news (i.e. when the incumbent demonstrates competence) is greater than the electoral effect of worse-than-expected news (i.e. when the incumbent demonstrates incompetence). For this reason, a uniform distribution of ideological I I biases implies that E[VS ] − E[VN ] = 0. Similar results could be obtained using variants of this signaling model that are united by the occurrence of a homicide shock that reveals the incumbent’s type. For example, incumbents could invest in their capacity to respond to homicide shocks in advance, enabling voters to separate competent from less competent parties when a homicide shock reveals the investment.

A.2 Months and years of municipal elections

Table A1 reports the municipal elections potentially covered by the survey and aggregate elections in the main analysis.

A7 Table A1: Municipal elections, 1999-2013, by state

State Election dates Aguascalientes August 2001, August 2004, August 2007, July 2010, July 2013. Baja California June 2001, August 2004, August 2007, July 2010, July 2013. Baja California Sur February 1999, February 2002, February 2005, February 2008, February 2011. Campeche July 2000, July 2003, July 2006, July 2009, July 2012. Chiapas October 2001, October 2004, October 2007, July 2010, July 2012. Chihuahua July 2001, July 2004, July 2007, July 2010, July 2013. Coahuila September 1999, September 2002, September 2005, October 2008, July 2010, July 2013. Colima July 2000, July 2003, July 2006, July 2009, July 2012. Distrito Federal July 2000, July 2003, July 2006, July 2009, July 2012. Durango July 2001, July 2004, July 2007, July 2010, July 2013. Guanajuato July 2000, July 2003, July 2006, July 2009, July 2012. Guerrero October 1999, October 2002, October 2005, October 2008, July 2012. Hidalgo November 1999, November 2002, November 2005, November 2008, July 2011. Jalisco November 2000, July 2003, July 2006, July 2009, July 2012. Estado de Mexico´ July 2000, March 2003, March 2006, July 2009, July 2012. Michoacan´ November 2001, November 2004, October 2007, October 2011. Morelos July 2000, July 2003, July 2006, July 2009, July 2012. Nayarit July 1999, July 2002, July 2005, July 2008, July 2011. Nuevo Leon´ July 2000, July 2003, July 2006, July 2009, July 2012. Oaxaca August 2001, August 2004, August 2007, July 2010, July 2013. Puebla November 2001, November 2004, November 2007, July 2010, July 2013. Queretaro´ July 2000, July 2003, July 2006, July 2009, July 2012. Quintana Roo February 1999, February 2002, February 2005, February 2008, July 2010, July 2013. San Luis Potos´ı July 2000, July 2003, July 2006, July 2009, July 2012. Sinaloa November 2001, November 2004, October 2007, July 2010, July 2013. Sonora July 2000, July 2003, July 2006, July 2009, July 2012. Tabasco October 2000, October 2003, October 2006, October 2009, July 2012. Tamaulipas October 2001, November 2004, November 2007, July 2010, July 2013. Tlaxcala November 2001, November 2004, October 2007, July 2010, July 2013. Veracruz September 2000, September 2004, September 2007, July 2010, July 2013. Yucatan´ May 2001, May 2004, May 2007, May 2010, July 2012. Zacatecas July 2001, July 2004, July 2007, July 2010, July 2013.

Notes: Emboldened election are counted as upcoming local elections in the survey analysis. State-level elections were held in Hidalgo in February 2002 without concurrent municipal elections, and are counted as upcoming local elections. Italicized elections are not included in the sample for the homicide shocks analysis due to data unavailability (or exclusion in the case of the Federal District). Except in the cases of Baja California 2001 and 2004 and Oaxaca 2013, missingness reﬂects the fact that data from the preceding election required to deﬁne the change in vote share was not available. For Baja California 2001 and 2004, the precinct numbering changed across elections and thus cannot be matched. For Oaxaca 2013, precinct level data was unavailable.

A8 A.3 Data description

A.3.1 ENCUP survey data

Upcoming local election. Indicator coded 1 for respondents living in a state/municipality with an upcoming local election occurring within the year of the survey. States/municipalities where an election has already occurred within the year of the survey are coded 0. Watch and listen to news and political programs ever/monthly/weekly/daily. Indicator coded 1 for a respondent that answers that they watch political programs or listen to news at least ever/once a month/at least once a week/daily. (“¿Que´ tan seguido escucha noticias o ve programas sobre pol´ıtica?”) Watch and listen to news and political programs scale. 5-point scale from 0 to 4, with values corresponding to levels of watching and listening to new and political programs (in ascending order). Topical political knowledge. First factor from a factor analysis containing the following questions: What is the name of the youth movement that recently started in Mexico? (2012) Where was the plan to build an airport that was subsequently abandoned due to local pressure? (2003, 2005) Which political party intends to charge VAT on medicines, food, and tuition? (2001) Which party holds your state governorship? (2001, 2003, 2005, 2012) What is the name of your state Governor? (2001) Education. 5-point variable, where 0 is less than completed primary education, 1 is a maximum education level of completing high school, 2 is a maximum level of completing lower secondary education, 3 is a maximum level of complete secondary education (preparatoria), and 4 is at least a university degree. Homicide shock. This indicator is coded 1 if either the number of homicides in the two months prior to the month of the survey (including the survey month) or the two months prior to the survey month exceed those in the two months immediately after the month of the survey, based on the INEGI monthly homicide statistics for the occurrence of homicides among a municipality’s residents. In 2005, the indicator is coded using the current month if the day of the month is greater than the 16th. (Note that homicides figures are subject to reclassification across time.) Homicides last year. Average number of residents suffering a homicide per month within the municipality in the preceding 12 months (excluding the current month). (Note that homicides figures are subject to reclassification across time.) Homicides last 3 years. Average number of residents suffering a homicide per month within the municipality in the preceding 36 months (excluding the current month). (Note that homicides

A9 figures are subject to reclassification across time.) Public insecurity the major problem in the community. Indicator coded 1 if, in an open response, a respondent lists violence, crime or public security as the main problem facing their community (including as 0s respondents that listed no problem). Low confidence in mayor. Indicator coded 1 for respondents answering that their confidence in the municipal mayor is 5 or below on a scale from 0 to 10 (for the 2003, 2005, and 2012 surveys) or expressing no or almost no confidence in the municipal mayor (in 2001), in response to a question asking about the level of confidence that respondents have in the listed institutions. Number of organizations. The number of organizations that a respondent reports being a member of, or previously being a member of. The number of possible organizations slightly varies across survey. Organizations talk about politics. Indicator coded 1 for respondents that answer that politics is discussed at the organizations they are a member of. Number of group meetings. The number of political organizations at which an individual has attended a meeting during the last year. Discuss community problems. A scale measuring the regularity with which respondents discuss problems in the community with friends and neighbors, ranging through never (coded 0), occasionally (coded 1) and frequently (coded 2). Incumbent win margin (lag). The difference in vote share between the incumbent and second- placed finisher at the previous municipal mayoral election (or an election held later in the year of the survey). In Usos y Custombres in Oaxaca, the incumbent win margin is set to the maximum of 1. ENPV (lag). The effective number of political parties (by vote share) at the previous municipal mayoral election (or an election held later in the year of the survey). In Usos y Custombres in Oaxaca, ENPV is set to the maximum of 1. Incumbent won (lag). Indicator coded 1 for municipalities where the incumbent party was re-elected at the most recent election (or an election held later in the year of the survey). Incumbent vote share (lag). The municipal vote share of the incumbent party at the most recent election (or an election held later in the year of the survey). Police per voter (lag). Total number of municipal security employees in the previous year (in thousands), divided by the total number of registered voters.

A10 A.3.2 Precinct and municipal homicide and electoral data

Change in incumbent party vote share. Change in the precinct-level share of all votes cast for the incumbent between the current municipal election and the prior municipal election (3 or 4 years earlier). When multiple parties form an incumbent coalition, the incumbent vote share is determined by the vote share of the largest party/coalition containing an incumbent party at the next election in terms of vote share. Incumbent party win. Indicator coded 1 if the incumbent party wins the municipal election. In the case of coalitions, is defined similarly to the above. Change in turnout. Change in the precinct-level turnout rate between the current municipal election and the prior municipal election (3 or 4 years earlier). Change in incumbent vote share (registered). Change in the precinct-level share of votes, as a share of all registered voters, cast for the incumbent between the current municipal election and the prior municipal election (3 or 4 years earlier). Homicide shock. Defined in equation (2) of the main paper, using INEGI homicide statistics for intentional homicides that occurred in each month to residents of a given municipality. One- and three-month versions are similarly defined. (Note that homicides figures are subject to reclassification across time.) Placebo homicide shock (6 months earlier). Defined as in equation (2) of the main paper, with the exception that all months are shifted 6 months forward in time. (Note that homicides figures are subject to reclassification across time.) Average monthly homicide rate (12 months/3 years before election). Average number of residents suffering a homicide per month within the municipality in the 12 months/3 years prior to the municipal election, again based on INEGI homicide data. (Note that homicides figures are subject to reclassification across time.) Post-2006. Indicator coded 1 for elections held since December 2006. No municipal police force. Indicator coded 1 for municipalities without a municipal police force under its direct control. This category includes municipalities that work solely with state police or federal police, work with the community, run security using a private or other service, or have no service at all. Municipalities that share police forces or use civil associations were excluded because channels of accountability are hard to discern. These categorizations were homogenized across the 2000, 2002, 2004, 2011 and 2013 ENGM surveys. Missing years were imputed according to the following rules: I first used the last available data, and if no previous coding was available took the nearest year in the future. Calderon´ Presidency. Indicator coded one for elections in the years 2007-2012.

A11 PAN/PRD. Indicator coded 1 for PAN/PRD municipal incumbents.

A.3.3 Precinct local media coverage data

Local media. Number of AM radio, FM radio or television stations, with an emitter based in the precinct’s municipality, covering at least 20% of the precinct population (as defined by detailed population data—block-level population in urban areas, and rural locality locations). Local AM radio/FM radio/television. Number of AM radio/FM radio/television stations, with an emitter based in the precinct’s municipal, covering at least 20% of the precinct population (as defined by detailed population data—block-level population in urban areas, and rural locality locations). Non-local media. Number of AM radio, FM radio or television stations, with an emitter based outside the precinct’s municipality, covering at least 20% of the precinct population (as defined by detailed population data—block-level population in urban areas, and rural locality locations). High higher education. Indicator coded 1 for electoral precincts where more than 40% of residents had experienced higher education in 2010, according to the 2010 Census.

A.4 Map of municipalities included in different samples

In separate ﬁgures, Figure A1 shades in red the municipalities that appear at least once in each of the main empirical analyses—the survey sample, the homicide shock sample, and the local media sample.

A.5 Additional analyses

The following subsections present the results of additional analyses cited in the main paper.

A.5.1 Assessing the identiﬁcation assumptions

Tables A2-A9 show the results of balance tests for the three main sets of empirical ﬁndings in the paper: Table A2 shows that upcoming local elections are well balanced across individual and municipal characteristics in the ENCUP survey data; Tables A6 and A7 shows that homicide shocks are well balanced across a wide variety of covariates, where municipality ﬁxed effects are excluded for time-invariant Census and geographic variables; and Table A9 shows that the number of local media stations is well-balanced across these same covariates. In addition, Tables A3 and A4 show that homicides and their interaction with upcoming local elections are well-balanced in the ENCUP surveys. Moreover, Table A5 demonstrates that neither

A12 (a) Municipalities in the ENCUP survey samples

(b) Municipalities in the homicide shock sample

Figure A1: Municipalities included in each empirical analysis (shaded in red)

A13 changes in upcoming local elections nor changes in measures of local violence predict whether a municipality is included in any given year. In each panel the outcome is an indicator for whether a municipality is included in that survey wave, conditional on a municipality appearing in at least one of the four ENCUP surveys. I also provide several additional tests to support the exogeneity of homicide shocks. First, Figure A2 shows that the distribution of homicides in months prior to the window used to define homicide shocks does not vary by whether a municipality ultimately experienced a homicide shock. For each set of months, Kolmogorov-Smirnov tests fail to reject the null of equality of distribution: respectively, the p-values associated with the combined test for 9 and 10 months before the election, 7 and 8 months before the election, 5 and 6 months before the election, and 3 and 4 months before the election are 0.998, 1.000, 0.335, and 0.856. Second, Table A8 shows that election outcomes are uncorrelated with homicide counts in the two months after elections. In particular, columns (3) and (4) find no correlation between the identity of the winning party and post-election homicides either throughout the sample or during the Calderon´ administration. This does not conflict with Dell(2015), who focuses on drug-related homicides over the subsequent mayor’s term, or as many months as possible of that mayor’s term.

A.5.2 Effects on turnout

Table A11 examines how homicide shocks affect turnout and incumbent vote share (as a proportion of registered voters). The results show that a homicide shock significantly increases turnout at the 90% level, but barely reduces incumbent vote shares, as a proportion of registered voters. Together, these results suggest that the decline in incumbent vote share (as a proportion of those that turned out) principally reflects a rise in turnout for non-incumbent parties. The sample sizes are slightly smaller than reported in the main text because turnout at the previous election is not always available, and thus the outcome cannot be constructed for some cases. Column (1) demonstrates that the overall effect on vote share continues to hold in this subsample. The results in Table A15 report the effect of drug-related homicide shocks just before an election, defined according to equation (2) but instead using drug-related homicides. Given that only five years of data exist, and thus many municipalities only appear once, I use state fixed effects instead of municipality fixed effects. Although the large drop in sample size unsurprisingly reduces precision substantially, the point estimates are similar to those reported in Table2. These findings reinforce the claim in the main text that voters respond similarly to different types of homicide.

A14 Table A2: Balance of upcoming local elections in the ENCUP surveys over 18 individual and municipal level variables

Observations 15,976 11,983 15,976 11,756 11,756 12,322 15,976 12,576 15,976 Outcome mean 0.55 0.81 40.76 1.70 0.47 1.57 1.06 0.26 1.52

A15 Local election mean 0.16 0.20 0.16 0.18 0.18 0.20 0.16 0.20 0.16 Discuss Homicide Homicide Homicide Incumbent ENPV Incumbent Incumbent Police community shock last year last 3 years win margin (lag) won vote share per voter problems (lag) (lag) (lag) (last year) (10) (11) (12) (13) (14) (15) (16) (17) (18) Upcoming local election 0.005 -0.022 1.607 1.607 0.022 0.011 0.094 0.012 -0.063 (0.029) (0.081) (1.080) (1.090) (0.016) (0.066) (0.064) (0.011) (0.178)

Observations 12,576 12,664 15,941 15,941 15,976 15,976 15,976 15,778 13,666 Outcome mean 0.70 0.44 4.50 4.82 0.15 2.57 0.61 0.48 2.30 Local election mean 0.20 0.17 0.16 0.16 0.16 0.16 0.16 0.17 0.16

Notes: All speciﬁcations include survey year ﬁxed effects, and are estimated using OLS. Standard errors clustered by municipality in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01. Table A3: Balance of homicide shock in the ENCUP surveys over 18 individual and municipal level variables

Female Catholic Age Education Employed Own econ. Number Org.s Number last year in month of talk about of group org.s politics meetings (1) (2) (3) (4) (5) (6) (7) (8) (9) Homicide shock -0.002 -0.008 -0.267 -0.010 -0.006 0.024 0.026 -0.010 0.029 (0.007) (0.012) (0.273) (0.053) (0.012) (0.016) (0.064) (0.014) (0.062)

Observations 12,664 9,522 12,664 9,464 9,464 9,591 12,664 9,764 12,664 Outcome mean 0.55 0.81 40.58 1.79 0.47 1.57 1.05 0.26 1.45

A16 Homicide shock mean 0.44 0.44 0.44 0.45 0.45 0.46 0.44 0.46 0.44 Discuss Upcoming Homicide Homicide Incumbent ENPV Incumbent Incumbent Police community local last year last 3 years win margin (lag) won vote share per voter problems election (lag) (lag) (lag) (last year) (10) (11) (12) (13) (14) (15) (16) (17) (18) Homicide shock -0.015 -0.010 -2.357* -3.143* 0.002 -0.032 -0.000 0.004 -0.139 (0.020) (0.036) (1.267) (1.860) (0.010) (0.042) (0.041) (0.006) (0.106)

Observations 9,764 12,664 12,664 12,664 12,664 12,664 12,521 12,606 10,584 Outcome mean 0.69 0.17 5.62 6.03 0.15 2.56 0.54 0.48 2.17 Homicide shock mean 0.46 0.44 0.44 0.44 0.44 0.44 0.44 0.44 0.45

Notes: All speciﬁcations include survey year ﬁxed effects, and are estimated using OLS. Standard errors clustered by municipality in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01. Table A4: Interactive balance of upcoming local election and homicide shock in the ENCUP surveys over 17 individual and municipal level variables

Female Catholic Age Education Employed Own econ. Number Org.s Number last year in month of talk about of group org.s politics meetings (1) (2) (3) (4) (5) (6) (7) (8) (9) Upcoming local election -0.007 -0.028 -0.458 0.156 -0.007 -0.012 -0.076 -0.039 -0.092 (0.018) (0.031) (0.595) (0.116) (0.025) (0.034) (0.108) (0.028) (0.123) Homicide shock -0.005 -0.017 -0.307 -0.015 -0.003 0.033* 0.060 -0.008 0.068 (0.008) (0.013) (0.319) (0.061) (0.014) (0.020) (0.068) (0.015) (0.060) Homicide shock 0.022 0.042 0.218 0.023 -0.014 -0.043 -0.215* -0.014 -0.249 × Upcoming local election (0.023) (0.032) (0.859) (0.160) (0.032) (0.047) (0.128) (0.032) (0.188)

Observations 12,664 9,522 12,664 9,464 9,464 9,591 12,664 9,764 12,664 Outcome mean 0.55 0.81 40.58 1.79 0.47 1.57 1.05 0.26 1.45

A17 Upcoming local election mean Homicide shock mean Discuss Upcoming Homicide Homicide Incumbent ENPV Incumbent Incumbent Police community local last year last 3 years win margin (lag) won vote share per voter problems election (lag) (lag) (lag) (last year) (10) (11) (12) (13) (14) (15) (16) (17) Upcoming local election -0.031 -0.429 -1.097 0.056** 0.071 0.159* 0.008 -0.157 (0.047) (1.504) (1.748) (0.023) (0.095) (0.091) (0.017) (0.257) Homicide shock -0.009 -3.110* -4.139* 0.009 -0.018 0.020 0.003 -0.176 (0.025) (1.585) (2.267) (0.012) (0.053) (0.048) (0.008) (0.123) Homicide shock -0.031 4.610** 6.067** -0.036 -0.085 -0.110 0.004 0.210 × Upcoming local election (0.056) (2.256) (2.816) (0.035) (0.126) (0.139) (0.025) (0.332)

Observations 9,764 12,664 12,664 12,664 12,664 12,521 12,606 10,584 Outcome mean 0.69 5.62 6.03 0.15 2.56 0.54 0.48 2.17 Upcoming local election mean Homicide shock mean

Notes: All speciﬁcations include survey year ﬁxed effects, and are estimated using OLS. Standard errors clustered by municipality in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01. Table A5: Predictors of municipalities included in each survey wave

Panel A: Linear predictors Surveyed municipality indicator (1) (2) (3) (4) (5) Local election 0.016 (0.037) Homicide within last month -0.020 (0.039) Homicide shock 0.036 (0.039) Homicides last year -0.001 (0.001) Homicides last 3 years -0.000 (0.001)

Observations 2,092 2,088 1,351 2,088 2,088 Outcome mean 0.46 0.46 0.52 0.46 0.46 Panel B: Election-homicide interactions Surveyed municipality indicator (1) (2) (3) (4) Local election 0.032 0.050 0.021 0.020 (0.055) (0.075) (0.042) (0.042) Homicide within last month -0.017 (0.040) Local election × Homicide within last month -0.029 (0.070) Homicide shock 0.052 (0.043) Local election × Homicide shock -0.124 (0.102) Homicides last year -0.001 (0.001) Local election × Homicides last year -0.003 (0.004) Homicides last 3 years -0.000 (0.001) Local election × Homicides last 3 years -0.002 (0.004)

Observations 2,088 1,351 2,088 2,088 Outcome mean 0.46 0.52 0.46 0.46

Notes: All speciﬁcations include municipality and survey-year ﬁxed effects, and are estimated using OLS. Stan- dard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01.

A18 Table A6: Municipal-level balance on 99 variables over pre-election homicide shocks

Outcome Effect of homicide shock Outcome Effect of homicide shock Coef. SE Obs. Coef. SE Obs. Electorate 5,003.795 (4,685.159) 2,852 Victims with complete primary schooling before election 0.874 (6.664) 1,658 Electorate density (log) -0.010 (0.010) 2,837 Victims with incomplete secondary schooling before election 1.270 (4.129) 1,658 Incumbent vote share (lag) 0.000 (0.007) 2,815 Victims with complete secondary schooling before election 0.943 (4.001) 1,658 Incumbent win (lag) 0.040 (0.042) 2,332 Single victims before election -0.037 (3.442) 1,698 Win margin (lag) 0.004 (0.011) 2,815 Job-related homicides before election 0.934 (1.004) 1,217 ENPV (lag) -0.021 (0.037) 2,852 Organs examined after homicide before election 2.247 (6.832) 1,562 Turnout (lag) -0.017** (0.008) 2,644 Family-incident homicides before election 0.050 (0.061) 1,737 PRI incumbent -0.076* (0.039) 2,852 Urban homicide victims before election 1.245 (7.528) 1,385 PAN incumbent 0.053 (0.040) 2,852 Non-Mexican homicide victims before election -0.031 (0.114) 1,792 PRD incumbent 0.024 (0.030) 2,852 Neighbor average homicide shock 0.004 (0.027) 2,739 Mayor’s party aligned with President 0.070* (0.037) 2,852 Average non-homicide deaths (prior 3 years) -2.700 (2.020) 2,852 Mayor’s party aligned with Governor -0.082** (0.041) 2,852 Average non-homicide deaths (prior year) -4.073* (2.248) 2,852 Mayor’s party aligned with President and Governor 0.008 (0.023) 2,852 Average child mortalities (prior 3 years) -0.051 (0.258) 2,124 Total municipal spending 23.572 (66.800) 1,759 Average child mortalities (prior year) 0.180 (0.028) 2,124 Police per voter 0.054 (0.070) 2,852 Area (km2) 417.555* (233.087) 2,852 Homicides 12 months before election -2.130 (2.310) 2,852 Local media -1.205 (1.217) 2,849 Homicides 11 months before election -1.628 (2.822) 2,852 Non-local media 0.005 (1.350) 2,849 Homicides 10 months before election -2.336 (2.644) 2,852 Occupants per room 0.004 (0.013) 2,826 Homicides 9 months before election -2.197 (2.546) 2,852 Share with 2 bedrooms -0.009 (0.008) 2,826 Homicides 8 months before election -2.988 (2.031) 2,852 Share 3+ bedrooms -0.008 (0.008) 2,826 Homicides 7 months before election -2.085 (2.210) 2,852 Share female 0.000 (0.001) 2,826 Homicides 6 months before election -2.004 (2.400) 2,852 Share working age 0.000 (0.002) 2,826 Homicides 5 months before election -1.542 (1.721) 2,852 Children per woman 0.000 (0.019) 2,826 Homicides 4 months before election -0.775 (2.176) 2,852 Female years of schooling 0.003 (0.086) 2,826 Homicides 3 months before election -1.066 (2.272) 2,852 Male years of schooling -0.010 (0.092) 2,826 Average homicides (prior 3 years) -0.763 (1.466) 2,852 Share illiterate 0.001 (0.003) 2,826 Average homicides (prior year) -1.875 (2.258) 2,852 Share economically active -0.003 (0.003) 2,826 Top homicide quartile (prior year) 0.007 (0.033) 2,852 Share born out of state -0.003 (0.015) 2,826 Top homicide decile (prior year) 0.006 (0.021) 2,852 Share Catholic 0.001 (0.005) 2,826 Presence of DTO 0.006 (0.031) 2,017 Share indigenous speakers 0.002 (0.003) 2,826 Average drug-related homicides (prior year) 0.006 (0.011) 2,852 Share without health care 0.000 (0.006) 2,826 Reports of inter-DTO violence before election -0.494 (0.817) 1,924 Share with electricity, running water, and drainage -0.010 (0.009) 2,826 Reports of violent enforcement before election 0.026 (0.108) 1,924 Share washing machine -0.012 (0.010) 2,826 Reports of arrests before election 0.083 (0.772) 1,924 Share landline telephone -0.012 (0.015) 2,826 Reports of drug seizures before election 0.575 (1.073) 1,924 Share radio -0.004 (0.007) 2,826 Reports of asset seizures before election -0.340 (0.262) 1,924 Share fridge -0.006 (0.008) 2,826 Reports of gun seizures before election 0.464 (0.450) 1,924 Share cell phone -0.004 (0.010) 2,826 Gun-related homicides before election -0.261 (5.383) 2,852 Share television -0.002 (0.003) 2,826 Chemical substance-related homicides before election -0.028 (0.017) 2,852 Share car or truck -0.005 (0.010) 2,826 Hanging-related homicides before election 0.137 (0.198) 2,852 Share computer -0.006 (0.011) 2,826 Drowning-related homicides before election 0.111*** (0.039) 2,852 Share internet -0.005 (0.010) 2,826 Explosives-related homicides before election 0.005 (0.005) 2,852 Nonhomicide crimes shock 0.126 (0.086) 591 Smoke/ﬁre-related homicides before election 0.033 (0.032) 2,852 Sexual assault shock 0.140 (0.101) 338 Cutting object-related homicides before election 0.648*** (0.221) 2,852 Kidnapping shock -0.191 (0.150) 104 Blunt object-related homicides before election 0.154* (0.080) 2,852 Robbery shock 0.127 (0.082) 556 Delayed homicide registrations before election 1.755 (5.769) 2,852 Carjacking shock 0.168 (0.124) 140 Male homicide victims before election 1.663 (6.323) 1,792 Criminal injury shock 0.073 (0.087) 517 Age of homicide victims before election 1.529*** (0.584) 1,749 Property theft shock -0.055 (0.090) 531 Victims with no schooling before election 0.322 (0.288) 1,658 Other crime shock 0.229*** (0.081) 576 Victims with incomplete primary schooling before election 1.322 (7.061) 1,658

Notes: Specifications include municipality and year fixed effects (unless otherwise stated), and are estimated using OLS. The time- invariant variables—area, media coverage, and the 2010 Census variables (occupants per dwelling-share internet)—and pre-election shocks regarding other types of crime (data are only available from 2011 onwards) exclude municipality fixed effects. Standard errors clustered by municipality in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01.

A19 Table A7: Precinct-level balance over 105 variables by pre-election homicide shocks

Outcome Effect of homicide shock Outcome Effect of homicide shock Coef. SE Obs. Coef. SE Obs. Electorate 81.500 (53.762) 167,116 Age of homicide victims before election 1.4822** (0.581) 144,229 Municipal electorate 5,088.790 (4,737.408) 167,116 Victims with no schooling before election 0.320 (0.288) 141,789 Electorate density (log) -0.005 (0.007) 164,722 Victims with incomplete primary schooling before election 1.282 (7.135) 141,789 Incumbent vote share (lag) 0.000 (0.007) 167,116 Victims with complete primary schooling before election 0.834 (6.732) 141,789 Municipal-level incumbent vote share (lag) 0.000 (0.007) 166,238 Victims with incomplete secondary schooling before election 1.253 (4.169) 141,789 Incumbent win (lag) 0.042 (0.042) 139,407 Victims with complete secondary schooling before election 0.921 (4.040) 141,789 Win margin (lag) 0.001 (0.009) 167,116 Single victims before election -0.063 (3.483) 142,988 Municipal-level win margin (lag) 0.004 (0.011) 166,238 Job-related homicides before election 0.935 (1.005) 126,754 Municipal-level ENPV (lag) -0.019 (0.032) 167,113 Organs examined after homicide before election 2.216 (6.894) 138,468 ENPV (lag) -0.020 (0.036) 167,116 Family-incident homicides before election 0.050 (0.061) 142,454 Turnout (lag) -0.0178** (0.007) 157,893 Urban homicide victims before election 1.178 (7.617) 123,125 Municipal-level turnout (lag) -0.0175** (0.007) 157,290 Non-Mexican homicide victims before election -0.034 (0.115) 145,210 PRI incumbent -0.0741* (0.039) 167,116 Neighbor average homicide shock 0.003 (0.027) 163,862 PAN incumbent 0.053 (0.039) 167,116 Average non-homicide deaths (prior 3 years) -2.746 (2.025) 167,116 PRD incumbent 0.023 (0.030) 167,116 Average non-homicide deaths (prior year) -4.1205* (2.249) 167,116 Mayor’s party aligned with President 0.0695* (0.037) 167,116 Average child mortalities (prior 3 years) -0.047 (0.258) 134,190 Mayor’s party aligned with Governor -0.0848** (0.040) 167,116 Average child mortalities (prior year) 0.183 (0.282) 134,190 Mayor’s party aligned with President and Governor 0.006 (0.023) 167,116 Area (km2) 4.6625* (2.539) 164,722 Total municipal spending 23.217 (66.622) 111,360 Local media -1.250 (1.217) 165,079 Police per voter 0.058 (0.070) 167,116 Non-local media 0.103 (1.368) 165,079 Homicides 12 months before election -2.117 (2.330) 167,116 Occupants per room 0.004 (0.013) 166,783 Homicides 11 months before election -1.632 (2.854) 167,116 Share with 2 bedrooms -0.007 (0.008) 166,653 Homicides 10 months before election -2.338 (2.672) 167,116 Share 3+ bedrooms -0.007 (0.008) 166,653 Homicides 9 months before election -2.217 (2.577) 167,116 Share female 0.000 (0.001) 166,664 Homicides 8 months before election -2.996 (2.052) 167,116 Share working age 0.000 (0.002) 166,664 Homicides 7 months before election -2.100 (2.229) 167,116 Children per woman 0.002 (0.018) 166,783 Homicides 6 months before election -2.013 (2.418) 167,116 Female years of schooling -0.001 (0.090) 166,783 Homicides 5 months before election -1.535 (1.737) 167,116 Male years of schooling -0.015 (0.097) 166,783 Homicides 4 months before election -0.766 (2.199) 167,116 Share illiterate 0.001 (0.003) 166,653 Homicides 3 months before election -1.050 (2.294) 167,116 Share economically active -0.003 (0.003) 166,664 Average homicides (prior 3 years) -0.763 (1.480) 167,116 Share born out of state -0.004 (0.013) 166,664 Average homicides (prior year) -1.876 (2.282) 167,116 Share Catholic 0.002 (0.005) 166,664 Top homicide quartile (prior year) 0.007 (0.033) 167,116 Share indigenous speakers 0.002 (0.003) 166,653 Top homicide decile (prior year) 0.006 (0.021) 167,116 Share without health care -0.001 (0.006) 166,664 Presence of DTO 0.006 (0.031) 131,039 Share with electricity, running water, and drainage -0.010 (0.009) 166,653 High-risk electoral precinct 0.002 (0.003) 50,392 Share washing machine -0.011 (0.010) 166,653 Average drug-related homicides (prior year) 0.006 (0.011) 167,116 Share landline telephone -0.012 (0.014) 166,653 Reports of inter-DTO violence before election -0.481 (0.827) 126,996 Share radio -0.004 (0.006) 166,653 Reports of violent enforcement before election 0.031 (0.109) 126,996 Share fridge -0.006 (0.008) 166,653 Reports of arrests before election 0.111 (0.786) 126,996 Share cell phone -0.004 (0.010) 166,653 Reports of drug seizures before election 0.619 (10.900) 126,996 Share television -0.002 (0.003) 166,653 Reports of asset seizures before election -0.329 (0.264) 126,996 Share car or truck -0.005 (0.010) 166,653 Reports of gun seizures before election 0.488 (0.458) 126,996 Share computer -0.007 (0.011) 166,653 Gun-related homicides before election -0.257 (5.449) 167,116 Share internet -0.006 (0.010) 166,653 Chemical substance-related homicides before election -0.0286* (0.017) 167,116 Nonhomicide crimes shock 0.126 (0.088) 32,770 Hanging-related homicides before election 0.130 (0.198) 167,116 Sexual assault shock 0.134 (0.103) 25,513 Drowning-related homicides before election 0.1107*** (0.039) 167,116 Kidnapping shock -0.176 (0.148) 13,005 Explosives-related homicides before election 0.005 (0.005) 167,116 Robbery shock 0.142* (0.085) 32,558 Smoke/ﬁre-related homicides before election 0.032 (0.032) 167,116 Carjacking shock 0.180 (0.128) 7,450 Cutting object-related homicides before election 0.6499*** (0.223) 167,116 Criminal injury shock 0.071 (0.089) 31,818 Blunt object-related homicides before election 0.1557* (0.080) 167,116 Property theft shock -0.075 (0.091) 31,608 Delayed homicide registrations before election 1.752 (5.840) 167,116 Other crime shock 0.245*** (0.082) 32,738 Male homicide victims before election 1.626 (6.395) 145,210

Notes: Specifications include municipality and year fixed effects, and are estimated using OLS. The time-invariant variables—area, media coverage, and the 2010 Census variables (occupants per dwelling-share internet)—exclude municipality fixed effects. Standard errors clustered by municipality in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01.

A20 Density 0 .05 .1 .15 .2 iueA:Dsrbto fpeeeto oiie,b oiiesokstatus shock homicide by homicides, pre-election of Distribution A2: Figure 0 Months 3and4beforeelection(shocked) Months 5and6beforeelection(shocked) Months 7and8beforeelection(shocked) Months 9and10beforeelection(shocked) 5 Average numberofhomicidespermonth 10 A21 Months 3and4afterelection(notshocked) Months 5and6afterelection(notshocked) Months 7and8beforeelection(notshocked) Months 9and10beforeelection(notshocked) 15 20 25 Table A8: Correlation between election outcomes and post-election homicides

Average homicides in the two months after an election (1) (2) (3) (4) Incumbent party win 4.309 (7.287) Change in incumbent party vote share -7.643 (6.249) PAN win 0.134 -19.256 (4.931) (14.469) PRI win 1.151 1.867 (3.805) (10.776) PRD win -8.705 -13.488 (8.283) (29.500)

Observations 2,852 173,389 2,852 975 Unique municipalities 906 1,329 906 484 Outcome mean 19.54 18.99 19.54 30.33 Election outcome mean 0.55 -0.05

Notes: All speciﬁcations include municipality and year ﬁxed effects, and are estimated using OLS. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01.

A.5.3 Additional robustness checks for the aggregate electoral results

Table A12 shows that the information consumption results are robust to deﬁning upcoming local elections by any number of months between 1 and 12 before the election.

A.5.4 Additional robustness checks for the aggregate electoral results

Table A13 reports the results from Table2 using incumbent vote share instead of the difference in incumbent vote share with respect to the previous election. The results do not meaningfully differ. Table A14 similarly shows that the main results are robust to including municipalities without a police force.

A.5.5 Electoral effects of drug-related homicides

As noted in the main text, the Calderon´ government released monthly municipal data on the number of drug-related deaths between 2007 and 2011. However, there are data issues with such data. First, these numbers are contentious (see Heinle, Rodr´ıguez Ferreira and Shirk 2014), and do not

A22 Table A9: Precinct-level balance over 92 variables by the number of local media stations

Outcome Effect of local media Outcome Effect of local media Coef. SE Obs. Coef. SE Obs. Homicide shock 0.000 (0.000) 29,736 Gun-related homicides before election 0.009 (0.009) 29,736 Area (km2) -0.003 (0.006) 29,736 Chemical substance-related homicides before election 0.000 (0.000) 29,736 Electorate -28.851* (15.100) 29,736 Hanging-related homicides before election 0.000 (0.001) 29,736 Municipal electorate 30.425 (25.718) 29,736 Drowning-related homicides before election 0.000 (0.000) 29,736 Electorate density (log) -0.012 (0.009) 29,701 Explosives-related homicides before election NA NA 29,736 Distance from centroid to municipal head (log) -0.005 (0.003) 29,736 Smoke/ﬁre-related homicides before election 0.000 (0.000) 29,736 Non-local media -0.031 (0.239) 29,736 Cutting object-related homicides before election 0.000 (0.001) 29,736 Incumbent vote share (lag) -0.000 (0.000) 29,736 Blunt object-related homicides before election 0.000 (0.000) 29,736 Incumbent win (lag) -0.000 (0.000) 24,186 Delayed homicide registrations before election 0.010 (0.010) 29,736 Win margin (lag) -0.000 (0.001) 29,736 Male homicide victims before election 0.009 (0.009) 28,181 Municipality win margin (lag) 0.000 (0.000) 29,736 Age of homicide victims before election 0.246 (0.304) 27,930 ENPV (lag) 0.001 (0.002) 29,736 Victims with no schooling before election -0.000 (0.001) 27,931 Municipality ENPV (lag) 0.000 (0.000) 29,736 Victims with incomplete primary schooling before 0.007 (0.010) 27,931 Turnout (lag) 0.001 (0.000) 28,779 Victims with complete primary schooling before election 0.006 (0.009) 27,931 Municipality turnout (lag) -0.000** (0.000) 28,819 Victims with secondary schooling before election 0.004 (0.006) 27,931 PRI incumbent 0.000 (0.000) 29,736 Single victims before election 0.004 (0.004) 28,010 PAN incumbent -0.000 (0.000) 29,736 Job-related homicides before election 0.001 (0.001) 26,281 PRD incumbent -0.000 (0.000) 29,736 Organs examined after homicide before election 0.009 (0.010) 27,631 Mayor’s party aligned with President 0.000 (0.000) 29,736 Family-incident homicides before election 0.000 (0.000) 27,486 Mayor’s party aligned with Governor -0.000 (0.000) 29,736 Urban homicide victims before election 0.003 (0.008) 24,715 Mayor’s party aligned with President and Governor 0.000 (0.000) 29,736 Non-Mexican homicide victims before election 0.000 (0.000) 28,181 Total municipal spending 0.236 (0.271) 19,842 Neighbor average homicide shock 0.000 (0.000) 28,608 Police per voter 0.001** (0.000) 29,736 Average non-homicide deaths (prior 3 years) -0.027 (0.018) 29,736 Homicides 12 months before election 0.009 (0.008) 29,736 Average non-homicide deaths (prior year) -0.026 (0.018) 29,736 Homicides 11 months before election 0.009 (0.011) 29,736 Average child mortalities (prior 3 years) 0.000 (0.001) 23,080 Homicides 10 months before election 0.002 (0.006) 29,736 Average child mortalities (prior year) -0.000 (0.001) 23,080 Homicides 9 months before election 0.007 (0.007) 29,736 Occupants per room -0.004** (0.002) 29,736 Homicides 8 months before election 0.005 (0.006) 29,736 Share with 2 bedrooms 0.000 (0.001) 29,736 Homicides 7 months before election -0.004 (0.009) 29,736 Share 3+ bedrooms 0.001 (0.001) 29,736 Homicides 6 months before election 0.000 (0.010) 29,736 Share female 0.000 (0.000) 29,736 Homicides 5 months before election 0.003 (0.009) 29,736 Share working age -0.000 (0.000) 29,736 Homicides 4 months before election 0.004 (0.007) 29,736 Children per woman -0.003 (0.002) 29,736 Homicides 3 months before election 0.005 (0.006) 29,736 Female years of schooling 0.014 (0.011) 29,736 Average homicides (prior 3 years) 0.005 (0.005) 29,736 Male years of schooling 0.023** (0.012) 29,736 Average homicides (prior year) 0.004 (0.008) 29,736 Share illiterate -0.000** (0.000) 29,736 Top homicide quartile (prior year) -0.000 (0.000) 29,736 Share economically active 0.000 (0.000) 29,736 Top homicide decile (prior year) -0.000 (0.000) 29,736 Share born out of state 0.001 (0.001) 29,736 Average drug-related homicides (prior year) 0.000 (0.000) 29,736 Share Catholic 0.000 (0.001) 29,736 Presence of DTO -0.000 (0.000) 22,764 Share indigenous speakers 0.000 (0.000) 29,736 High-risk electoral precinct 0.002 (0.002) 7,370 Share without health care -0.000 (0.000) 29,736 Reports of inter-DTO violence before election -0.001 (0.002) 22,048 Share with electricity, running water, and drainage 0.002* (0.001) 29,736 Reports of violent enforcement before election -0.000 (0.000) 22,048 Share washing machine 0.001 (0.001) 29,736 Reports of arrests before election 0.002 (0.002) 22,048 Share fridge 0.001 (0.001) 29,736 Reports of drug seizures before election 0.001 (0.002) 22,048 Share cell phone 0.000 (0.001) 29,736 Reports of asset seizures before election -0.001 (0.001) 22,048 Share car or truck 0.001 (0.001) 29,736 Reports of gun seizures before election 0.000 (0.001) 22,048 Share computer 0.002* (0.001) 29,736

Notes: All speciﬁcations include neighbor group and year ﬁxed effects, and are estimated using OLS. All observations are weighted by the number of registered voters divided by he number of comparison units within each neighbor group. There is no variation in the number of explosive-related homicides or non-homicide pre-election crime shocks (for which overlapping data are only available for one election) across local media in this sample. Standard errors clustered by municipality in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01.

A23 Table A10: Precinct-level balance over 92 variables by pre-election homicide shocks (in the local media sample)

Outcome Effect of homicide shock Outcome Effect of homicide shock Coef. SE Obs. Coef. SE Obs. Local media 0.005 (0.005) 29,736 Gun-related homicides before election -6.266 (14.269) 29,736 Area (km2) 0.001 (0.002) 29,736 Chemical substance-related homicides before election -0.014 (0.022) 29,736 Electorate 38.419 (47.667) 29,736 Hanging-related homicides before election -0.301 (0.542) 29,736 Municipal electorate 17,743.371** (6,872.275) 29,736 Drowning-related homicides before election 0.239** (0.097) 29,736 Electorate density (log) 0.014 (0.017) 29,701 Explosives-related homicides before election NA NA 29,736 Distance from centroid to municipal head (log) 0.000 (0.001) 29,736 Smoke/ﬁre-related homicides before election 0.046 (0.075) 29,736 Non-local media 0.001 (0.002) 29,736 Cutting object-related homicides before election 1.378** (0.598) 29,736 Incumbent vote share (lag) -0.004 (0.016) 29,736 Blunt object-related homicides before election 0.249 (0.205) 29,736 Incumbent win (lag) -0.115 (0.101) 24,186 Delayed homicide registrations before election -3.705 (15.418) 29,736 Win margin (lag) 0.012 (0.020) 29,736 Male homicide victims before election -4.803 (14.482) 28,181 Municipality win margin (lag) 0.024 (0.021) 29,736 Age of homicide victims before election -88.070 (496.152) 27,930 ENPV (lag) -0.022 (0.051) 29,736 Victims with no schooling before election 0.912 (0.598) 27,931 Municipality ENPV (lag) -0.013 (0.053) 29,736 Victims with incomplete primary schooling before -4.573 (15.258) 27,931 Turnout (lag) -0.002 (0.010) 28,779 Victims with complete primary schooling before election -5.087 (14.354) 27,931 Municipality turnout (lag) -0.003 (0.010) 28,819 Victims with secondary schooling before election -2.706 (8.637) 27,931 PRI incumbent 0.018 (0.064) 29,736 Single victims before election -3.689 (7.481) 28,010 PAN incumbent -0.008 (0.060) 29,736 Job-related homicides before election 1.929 (2.873) 26,281 PRD incumbent 0.000 (0.037) 29,736 Organs examined after homicide before election 0.391 (14.330) 27,631 Mayor’s party aligned with President 0.046 (0.062) 29,736 Family-incident homicides before election 0.008 (0.155) 27,486 Mayor’s party aligned with Governor -0.051 (0.065) 29,736 Urban homicide victims before election -3.839 (17.133) 24,715 Mayor’s party aligned with President and Governor 0.003 (0.018) 29,736 Non-Mexican homicide victims before election -0.180 (0.313) 28,181 Total municipal spending 253.374*** (79.149) 19,842 Neighbor average homicide shock -0.008 (0.063) 28,608 Police per voter 0.279* (0.164) 29,736 Average non-homicide deaths (prior 3 years) -4.047 (4.420) 29,736 Homicides 12 months before election -7.635 (6.711) 29,736 Average non-homicide deaths (prior year) -8.508 (5.308) 29,736 Homicides 11 months before election -6.272 (8.528) 29,736 Average child mortalities (prior 3 years) -0.439 (0.544) 23,080 Homicides 10 months before election -7.599 (7.421) 29,736 Average child mortalities (prior year) 0.389 (0.423) 23,080 Homicides 9 months before election -6.437 (7.299) 29,736 Occupants per room 0.000* (0.000) 29,736 Homicides 8 months before election -7.448 (5.702) 29,736 Share with 2 bedrooms -0.000** (0.000) 29,736 Homicides 7 months before election -0.980 (7.790) 29,736 Share 3+ bedrooms -0.001*** (0.000) 29,736 Homicides 6 months before election -3.042 (8.420) 29,736 Share female -0.000 (0.000) 29,736 Homicides 5 months before election -7.166 (5.596) 29,736 Share working age -0.000** (0.000) 29,736 Homicides 4 months before election -4.718 (6.179) 29,736 Children per woman -0.000 (0.001) 29,736 Homicides 3 months before election -3.315 (6.356) 29,736 Female years of schooling -0.002 (0.003) 29,736 Average homicides (prior 3 years) -3.308 (4.052) 29,736 Male years of schooling -0.001 (0.004) 29,736 Average homicides (prior year) -5.461 (6.719) 29,736 Share illiterate 0.000 (0.000) 29,736 Top homicide quartile (prior year) 0.035 (0.045) 29,736 Share economically active -0.000** (0.000) 29,736 Top homicide decile (prior year) 0.035 (0.045) 29,736 Share born out of state -0.000 (0.000) 29,736 Average drug-related homicides (prior year) 0.013 (0.017) 29,736 Share Catholic -0.000** (0.000) 29,736 Presence of DTO -0.049 (0.061) 22,764 Share indigenous speakers -0.000 (0.000) 29,736 High-risk electoral precinct -0.016 (0.011) 7,370 Share without health care 0.000 (0.000) 29,736 Reports of inter-DTO violence before election -1.724 (1.653) 22,048 Share with electricity, running water, and drainage 0.000 (0.000) 29,736 Reports of violent enforcement before election -0.075 (0.242) 22,048 Share washing machine -0.000 (0.000) 29,736 Reports of arrests before election 0.370 (2.089) 22,048 Share fridge 0.000 (0.000) 29,736 Reports of drug seizures before election 4.106 (4.027) 22,048 Share cell phone -0.000 (0.000) 29,736 Reports of asset seizures before election -0.190 (0.441) 22,048 Share car or truck 0.000 (0.000) 29,736 Reports of gun seizures before election -0.025 (0.602) 22,048 Share computer -0.000 (0.000) 29,736

A24 Table A11: Effect of pre-election homicide shocks on precinct-level turnout

Change in Change in Change in incumbent turnout incumbent party party vote share vote share (share of (share of turnout) registered voters) (1) (2) Homicide shock -0.022** 0.016* -0.004 (0.009) (0.009) (0.005)

Observations 157,893 157,893 157,893 Unique municipalities 905 905 905 Outcome range [-0.96,0.89] [-0.76,0.67] [-0.93,0.81] Outcome mean -0.06 0.00 -0.03 Homicide shock mean 0.42 0.42 0.42

Notes: All specifications are estimated using OLS, and include state and year fixed effects. All observations are weighted by the number of registered voters. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01. necessarily follow the homogeneous coroner’s report criteria used by INEGI. Second, the limited availability of this data, combined with the definition of a homicide shock that requires at least one drug-related death over the four-month window around elections, substantially reduces the sample size by around 75%. More generally, it is not clear theoretically whether voters should respond more or less to drug-related homicides, as opposed to other homicides. In fact, voters might think that these are less relevant to them than more arbitrary murders which constitute around 50% of totals homicides even during the drug war (only a tiny fraction of such homicides as domestic). Nevertheless, I use the drug-related homicide data as a robustness check. The results in Table A15 report the effect of drug-related homicide shocks just before an election, defined according to equation (2) but instead using drug-related homicides. Given that only five years of data exist, and thus many municipalities only appear once, I use state fixed effects instead of municipality fixed effects. Although the large drop in sample size unsurprisingly reduces precision substantially, the point estimates are similar to those reported in Table2. These findings reinforce the claim in the main text that voters respond similarly to different types of homicide.

A25 Table A12: The effect of upcoming local elections on political news consumption and topical political knowledge, by number of months before the election

Number of months before election used to deﬁne an upcoming local election 1 month 2 months 3 months 4 months 5 months 6 months 7 months 8 months 9 months 10 months 11 months 12 months (1) (2) (3) (4) (5) (6) (7) (8) (9) (10) (11) (12) Panel A: Outcome: Watch and listen to news and political programs ever Upcoming local election 0.093*** 0.093*** 0.067*** 0.067*** 0.049*** 0.049*** 0.059*** 0.061*** 0.061*** 0.062*** 0.044*** 0.044*** (0.015) (0.015) (0.013) (0.013) (0.014) (0.014) (0.013) (0.013) (0.013) (0.013) (0.010) (0.010)

Observations 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 Municipalities 539 539 539 539 539 539 539 539 539 539 539 539 Outcome range {0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1} Outcome mean 0.87 0.87 0.87 0.87 0.87 0.87 0.87 0.87 0.87 0.87 0.87 0.87 Local election mean 0.02 0.02 0.06 0.06 0.19 0.19 0.31 0.33 0.33 0.33 0.44 0.44 Panel B: Outcome: Watch and listen to news and political programs weekly Upcoming local election 0.116*** 0.116*** 0.105*** 0.105*** 0.082*** 0.082*** 0.092*** 0.088*** 0.088*** 0.092*** 0.091*** 0.091*** (0.038) (0.038) (0.032) (0.032) (0.022) (0.022) (0.019) (0.019) (0.019) (0.019) (0.016) (0.016)

Observations 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 Municipalities 539 539 539 539 539 539 539 539 539 539 539 539 A26 Outcome range {0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1} Outcome mean 0.63 0.63 0.63 0.63 0.63 0.63 0.63 0.63 0.63 0.63 0.63 0.63 Local election mean 0.02 0.02 0.06 0.06 0.19 0.19 0.31 0.33 0.33 0.33 0.44 0.44 Panel C: Outcome: Watch and listen to news and political programs scale Upcoming local election 0.416*** 0.416*** 0.373*** 0.373*** 0.276*** 0.276*** 0.327*** 0.319*** 0.319*** 0.327*** 0.306*** 0.306*** (0.122) (0.122) (0.106) (0.106) (0.075) (0.075) (0.062) (0.061) (0.061) (0.062) (0.050) (0.050)

Observations 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 13,030 Municipalities 539 539 539 539 539 539 539 539 539 539 539 539 Outcome range {0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1} Outcome mean 2.58 2.58 2.58 2.58 2.58 2.58 2.58 2.58 2.58 2.58 2.58 2.58 Local election mean 0.02 0.02 0.06 0.06 0.19 0.19 0.31 0.33 0.33 0.33 0.44 0.44 Panel D: Outcome: Topical political knowledge Upcoming local election 0.448*** 0.218** 0.403*** 0.403*** 0.312*** 0.312*** 0.265*** 0.245*** 0.224*** 0.212*** 0.149*** 0.149*** (0.119) (0.102) (0.085) (0.085) (0.051) (0.051) (0.045) (0.045) (0.043) (0.042) (0.032) (0.032)

Observations 17,213 17,213 17,213 17,213 17,213 17,213 17,213 17,213 17,213 17,213 17,213 17,213 Municipalities 539 539 539 539 539 539 539 539 539 539 539 539 Outcome range [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] [-2.11,1.56] Outcome mean 0.00 0.00 0.00 0.00 0.00 0.00 0.00 0.00 0.00 0.00 0.00 0.00 Local election mean 0.01 0.03 0.06 0.06 0.16 0.16 0.25 0.27 0.28 0.29 0.37 0.37

Notes: All speciﬁcations include survey-year ﬁxed effects, and are estimated using OLS. The outcomes in panels A-C were not collected in the 2001 survey. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01. Table A13: Effects of pre-election homicide shocks on municipal incumbent vote share

Baseline No ﬁxed Controls State- Incumbent Municipality Placebo Violence Fewer than Few Non- One- Three- Four- First Main Single- spec. effects year party -speciﬁc 6 months bin 25 homicides drug DTO month month month half of party party effects trends trends earlier effects per month homicides states shock shock shock month incumbent incumbent (1) (2) (3) (4) (5) (6) (7) (8) (9) (10) (11) (12) (13) (14) (15) (16) (17) Outcome: Incumbent party vote share Homicide shock -0.022*** -0.015** -0.015** -0.017*** -0.016** -0.026*** -0.025*** -0.020*** -0.022*** -0.018** -0.022*** -0.021*** -0.025*** (0.007) (0.007) (0.006) (0.006) (0.007) (0.009) (0.007) (0.007) (0.007) (0.009) (0.008) (0.007) (0.009) Placebo homicide 0.006 shock (0.010) Homicide shock -0.009 (one month) (0.009) Homicide shock -0.022*** (three month) (0.007) Homicide shock -0.025*** (four month) (0.008)

A27 Observations 167,116 173,115 162,774 167,116 157,639 167,116 145,511 167,116 157,555 167,116 102,126 143,840 180,302 188,067 152,539 157,639 104,220 Unique municipalities 906 1,335 895 906 823 906 820 906 905 906 616 637 1,064 1,172 854 823 641 Outcome mean 0.42 0.42 0.42 0.42 0.42 0.42 0.42 0.42 0.42 0.42 0.40 0.42 0.42 0.41 0.42 0.42 0.42 Outcome std. dev. 0.15 0.15 0.14 0.15 0.14 0.15 0.14 0.15 0.15 0.15 0.14 0.14 0.15 0.15 0.14 0.14 0.15 Homicide shock mean 0.41 0.42 0.41 0.41 0.42 0.47 0.41 0.41 0.42 0.41 0.41 0.48 0.43 0.42 0.41 0.42 0.39

Notes: Column (2) excludes municipality and year fixed effects, and thus includes municipalities 429 municipalities where a homicide shock is only defined for one election where electoral data is available. Columns (3) includes the controls in Table A6, with the exception of variables with greater than 5% missingness. Column (4) includes state-year fixed effects. Column (5) includes party-specific incumbent year trends. Column (6) includes municipality-specific year trends. Column (7) uses a placebo homicide shock defined six months before the election. Column (8) includes fixed effects for the total number of homicides over the four-month window in bins of size ten. Column (9) excludes municipalities averaging more than 25 homicides per month over the two months either before or after the election. Column (10) excludes municipalities that average more than one drug-related homicide a month over the 12 months before an election between 2006 and 2011. Column (11) excludes states with high-level of DTO activity (see footnote 43). Columns (12)-(14) respectively define homicide shocks over one-, three-, and four-month windows. Column (15) includes only elections that take place on or before the 15th of the month. Column (16) includes only elections where the PAN, PRD, or PRI are an incumbent. Column (17) includes only observations where the incumbent is not a coalition. All specifications are estimated using OLS, and all observations are weighted by the number of registered voters in the electoral precinct. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01. Table A14: Effects of pre-election homicide shocks on municipal incumbent electoral outcomes, including municipalities without a police force

Baseline No ﬁxed Controls State- Incumbent Municipality Placebo Violence Fewer than Few Non- One- Three- Four- First Main Single- spec. effects year party -speciﬁc 6 months bin 25 homicides drug DTO month month month half of party party effects trends trends earlier effects per month homicides states shock shock shock month incumbent incumbent (1) (2) (3) (4) (5) (6) (7) (8) (9) (10) (11) (12) (13) (14) (15) (16) (17) Panel A: Outcome: Incumbent party win Homicide shock -0.116*** -0.078** -0.080** -0.101*** -0.105*** -0.126** -0.127*** -0.103*** -0.116*** -0.112** -0.106*** -0.117*** -0.094* (0.034) (0.031) (0.034) (0.028) (0.037) (0.054) (0.032) (0.036) (0.034) (0.044) (0.037) (0.035) (0.052) Placebo homicide -0.021 shock (0.046) Homicide shock -0.037 (one month) (0.041) Homicide shock -0.102*** (three month) (0.037) Homicide shock -0.091** (four month) (0.037)

Observations 3,366 3,773 3,157 3,366 3,033 3,366 2,902 3,366 3,352 3,366 2,261 2,247 4,114 4,685 3,105 3,033 2,110 Unique municipalities 1,018 1,425 966 1,018 934 1,018 948 1,018 1,017 1,018 699 728 1,186 1,312 973 934 745 Outcome range {0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1}{0,1} Outcome mean 0.56 0.56 0.57 0.56 0.57 0.56 0.57 0.56 0.56 0.56 0.55 0.57 0.56 0.55 0.57 0.57 0.56 Homicide shock mean 0.41 0.41 0.41 0.41 0.41 0.45 0.41 0.41 0.41 0.41 0.41 0.48 0.43 0.42 0.41 0.41 0.38 Panel B: Outcome: Change in incumbent party vote share Homicide shock -0.022*** -0.018*** -0.013** -0.017*** -0.016** -0.027*** -0.025*** -0.022*** -0.022*** -0.022** -0.018** -0.021*** -0.029*** (0.008) (0.007) (0.006) (0.006) (0.008) (0.009) (0.008) (0.008) (0.008) (0.010) (0.008) (0.008) (0.011) Placebo homicide -0.007 A28 shock (0.010) Homicide shock -0.012 (one month) (0.010) Homicide shock -0.025*** (three month) (0.008) Homicide shock -0.027*** (four month) (0.008)

Observations 194,378 198,903 188,681 194,378 184,161 194,378 172,291 194,378 183,882 194,378 121,534 167,297 209,741 219,061 176,231 184,161 121,809 Unique municipalities 1,018 1,424 1,005 1,018 934 1,018 948 1,018 1,017 1,018 699 728 1,186 1,312 973 934 745 Outcome range [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.87] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] [-0.96,0.89] Outcome mean -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.05 -0.04 Outcome std. dev. 0.14 0.15 0.14 0.14 0.14 0.14 0.14 0.14 0.15 0.14 0.14 0.14 0.15 0.15 0.15 0.14 0.15 Homicide shock mean 0.41 0.41 0.41 0.41 0.41 0.47 0.41 0.41 0.41 0.41 0.41 0.48 0.43 0.42 0.41 0.41 0.38

Notes: Column (2) excludes municipality and year fixed effects, and thus includes municipalities 429 municipalities where a homicide shock is only defined for one election where electoral data is available. Columns (3) includes the controls in Table A6, with the exception of variables with greater than 5% missingness. Column (4) includes state-year fixed effects. Column (5) includes party-specific incumbent year trends. Column (6) includes municipality-specific year trends. Column (7) uses a placebo homicide shock defined six months before the election. Column (8) includes fixed effects for the total number of homicides over the four-month window in bins of size ten. Column (9) excludes municipalities averaging more than 25 homicides per month over the two months either before or after the election. Column (10) excludes municipalities that average more than one drug-related homicide a month over the 12 months before an election between 2006 and 2011. Column (11) excludes states with high-level of DTO activity (see footnote 43). Columns (12)-(14) respectively define homicide shocks over one-, three-, and four-month windows. Column (15) includes only elections that take place on or before the 15th of the month. Column (16) includes only elections where the PAN, PRD, or PRI are an incumbent. Column (17) includes only observations where the incumbent is not a coalition. All specifications are estimated using OLS, and all observations are weighted by the number of registered voters in the electoral precinct. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01. Table A15: Effect of pre-election drug-related homicide shocks on municipal incumbent electoral outcomes

Incumbent Change in party incumbent win party vote share (1) (2) Drug-related homicide shock -0.068 -0.020 (0.074) (0.017)

Observations 471 37,943 Unique municipalities 416 416 Outcome mean 0.53 -0.05 Homicide shock mean 0.44 0.44

A.5.6 Difference-in-differences approach to identifying the effects of pre-election homicides

The results in the main text focus on pre-election homicide shocks coded as a binary variable. This approach is theoretically appealing because its short-term nature both captures difference relative to the municipality’s general baseline as well as closely maps to cycles in political information consumption. Moreover it is empirically appealing because month-to-month variation in homicide shocks is both plausibly exogenous to a wide variety of possible confounds and uncorrelated with the broader trends in homicide rates that this article seeks to differentiate the effects of short-term spikes around elections from. However, I also now consider an alternative approach to capturing the effects of short-run shocks around local elections that does not rely on homicide data after the election. Since the homicide level, as opposed to the short-term deviation exploited in the main paper, just before an election is highly correlated with the general homicide level, a meaningful test of increased homicides around elections requires a subtler design.68 I thus use a difference-in- differences design to identify how deviations in the number of homicides just before elections, relative to the number of homicides occurring earlier in the electoral cycle, affect vote choice. Speciﬁcally,I ﬁrst use the raw difference between the average number of homicides in the two

68The results of such an approach are thus similar to the small long-run estimates reported in Table3.

A29 months prior to an election and the average number of homicides over the prior electoral cycle (i.e. preceding 34 months). A second measure then takes the proportional difference by normalizing these deviations by the average number of homicides over the prior electoral cycle. Finally, a third approach codes indicators for above- and below-median municipalities according to the two preceding variables. These measures seek to capture differences in the magnitude of pre-election homicide deviations across elections, and thus exploit variation in the intensity of these shocks across municipalities. The identifying assumption is that municipalities experiencing different homicide deviations from election cycle trends before elections otherwise follow parallel trends in incumbent support. Table A16 reports estimates from the analog of equation (4), and demonstrates that this alternative approach to capturing pre-election homicide deviations also decreases the incumbent party’s vote share. Although the estimates are often borderline statistically signiﬁcant, columns (1) and (2) ﬁrst show that an increase in the raw pre-election deviation decreases the probability of the incumbent winning and the incumbent’s vote share. This estimates are more precisely estimated when separating above and below median deviations in columns (3) and (4). Columns (5)-(8) report similar results when considering the proportional deviation instead.

A.5.7 Differential effects of homicide shocks across parties

I also examine differential punishment across parties. Due to the PRI’s more extensive clientelistic ties (e.g. Cornelius 1996; Fox 1994; Greene 2007; Magaloni 2006), PRI voters may be less susceptible to performance information, and thus less inclined to punish PRI incumbents for homicide shocks. Table A17 provides tentative evidence consistent with this expectation. Although the interaction terms are not statistically significant, column (1) shows that the PAN and PRD are punished relatively more than the PRI. Although punishment of PRI incumbents is not statistically significant, columns (2)-(4) register significant punishment of PAN and PRD mayors. This is potentially because the PAN and especially PRD control more urban areas where the effects of homicide shocks are larger. Finally, who do voters turn to in order to reduce local violence? If reducing violence is a major concern, and voters believe that Calderon’s´ tough stance on drug-related crime may help their municipality (see Dell 2015), even PAN mayors may benefit from a homicide shock. Column (5) of panel C finds suggestive evidence for this: although a homicide shock increases the PAN’s vote share by 4.6 percentage points during Calderon’s´ presidency, this interaction is not statistically significant.

A30 Table A16: Difference-in-differences approach to estimating the effect of pre-election deviations in homicide rates on municipal incumbent electoral outcomes

(1) (2) (3) (4) (5) (6) (7) (8) Panel A: Outcome: Incumbent party win Deviation from average monthly homicide -0.0016 -0.0077*** (0.0033) (0.0020) Above median deviation from average monthly homicide -0.0932** -0.0253 (0.0437) (0.0613) Proportional deviation from average monthly homicide -0.0176* -0.0250 (0.0094) (0.0168) Above median proportional deviation from average monthly homicide -0.1038** -0.0471 (0.0431) (0.0595)

Observations 2,852 2,852 2,852 2,852 2,808 2,808 2,808 2,808 Unique municipalities 906 906 906 906 887 887 887 887 Outcome mean 0.55 0.55 0.55 0.55 0.55 0.55 0.55 0.55 Homicide measure mean 1.67 1.67 0.50 0.50 0.32 0.32 0.50 0.50 A31 Homicide measure standard deviation 14.31 14.31 0.50 0.50 1.52 1.52 0.50 0.50 Panel B: Outcome: Change in incumbent party vote share Deviation from average monthly homicide -0.0006 -0.0008 (0.0004) (0.0005) Above median deviation from average monthly homicide -0.0305*** -0.0311** (0.0103) (0.0137) Proportional deviation from average monthly homicide -0.0024 -0.0041 (0.0020) (0.0035) Above median proportional deviation from average monthly homicide -0.0336*** -0.0339*** (0.0095) (0.0128)

Observations 167,116 167,116 167,116 167,116 166,892 166,892 166,892 166,892 Unique municipalities 906 906 906 906 905 905 905 905 Outcome mean 0.55 0.55 0.55 0.55 0.55 0.55 0.55 0.55 Homicide measure mean 1.70 1.70 0.50 0.50 0.33 0.33 0.50 0.50 Homicide measure standard deviation 14.39 14.39 0.50 0.50 1.54 1.54 0.50 0.50 Municipality-speciﬁc time trends XXXX

Notes: All speciﬁcations are estimated using OLS, and include municipality and year ﬁxed effects. All observations are weighted by the number of registered voters. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01. Table A17: Effects of pre-election homicide shocks on municipal incumbent electoral outcomes, by incumbent party

Change in Change in Change in Change in Change in incumbent PAN PRD PRI PAN party incumbent incumbent incumbent incumbent vote share vote share vote share vote share vote share (1) (2) (3) (4) (5) Homicide shock -0.007 -0.037*** -0.049* -0.009 0.026 (0.013) (0.012) (0.026) (0.013) (0.022) Homicide shock × PAN -0.016 (0.023) Homicide shock × PRD -0.046 (0.035) Homicide shock × Calderon´ 0.046 Presidency (0.044)

Observations 158,954 56,597 19,767 82,590 167,116 Unique municipalities 898 432 286 769 906 Outcome mean -0.05 -0.06 -0.09 -0.04 -0.05 Outcome standard deviation 0.14 0.14 0.17 0.13 0.14 Homicide shock mean 0.42 0.43 0.44 0.40 0.41

Notes: All speciﬁcations are estimated using OLS. All observations are weighted by the number of registered voters. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01.

A32 Table A18: Heterogeneous effects of upcoming local elections on institutional confidence at higher levels of government, by short-run homicide shocks Low confidence Low confidence in the President in state Governor (1) (2) (3) (4) Upcoming local election 0.064* 0.051* -0.059 0.064 (0.035) (0.030) (0.040) (0.089) Homicide shock -0.009 -0.010 -0.054** -0.032 (0.014) (0.012) (0.025) (0.020) Upcoming local election × Homicide shock 0.033 0.015 -0.001 -0.073 (0.040) (0.038) (0.061) (0.158)

Observations 13,551 13,551 6,445 6,445 Clusters 390 390 293 293 Outcome range {0,1}{0,1}{0,1}{0,1} Outcome mean 0.27 0.27 0.33 0.33 Local election mean 0.16 0.16 0.02 0.02 Homicide measure mean 0.45 0.45 0.42 0.42 Survey years without data 2003, 2005 2003, 2005 State fixed effects XX Notes: All specifications include survey year fixed effects, and are estimated using OLS. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01.

A.5.8 Belief updating about presidents and state governors

Table A18 extends the results of Table7 to higher-level of government. As noted in the main text, the results indicate that—in contrast with conﬁdence in their mayor—voters do not become less conﬁdent in the president or their state governor when they experience a pre-election homicide shock. This reinforces the responsibility attribution implied by Table5.

A.5.9 Differential updating across elections

Table A19 reports the regression estimates underlying Figure6.

A.5.10 Learning from the experiences of neighboring municipalities

To identify how comparative performance information inﬂuences voter behavior, I compute the average homicide shock across neighboring municipalities and the same average weighted by the size of neighboring municipalities’ registered electorates. Consistent with voters benchmarking

A33 Table A19: The effect of a homicide shock on the change in incumbent party vote share, by previous homicide shocks and incumbent identity

Change in incumbent party vote share (1) Homicide shock -0.040** (0.018) Homicide shock at last election -0.042* (0.025) Homicide shock × Homicide shock at last election 0.063** (0.031) Incumbent won previous election -0.046** (0.019) Homicide shock × Incumbent won previous election 0.013 (0.029) Homicide shock at last election × Incumbent won previous election 0.035 (0.031) Homicide shock × Homicide shock at last election -0.070 × Incumbent won previous election (0.045)

Observations 111,910 Unique municipalities 730 Outcome range [-0.90,0.89] Outcome mean -0.06 Outcome standard deviation 0.14 Homicide shock mean 0.43 Homicide shock at last election mean 0.40 Incumbent won previous election mean 0.55

Notes: All speciﬁcations include municipality and year ﬁxed effects, and are estimated using OLS. All observations are weighted by the number of registered voters. Standard errors clustered by municipality in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01.

A34 their incumbent’s performance against that of their neighbors, column (1) of Table A20 shows that the probability that an incumbent party is re-elected increases with the average shock experienced by neighboring municipalities. However, the negative interaction between the homicide shock and the neighbor average suggests that relative performance considerations do not apply when a voter’s own municipality is afﬂicted by a shock.69 Plausibly consistent with increased salience, mayoral punishment instead increases with the proportion of shocks experienced by neighbors. The change in vote share follows a similar pattern but is not statistically signiﬁcant, while columns (2) and (4) report similar results when an electorate-weighted neighboring municipal shock measure is used instead.

A.5.11 Less-educated voters respond most to pre-election homicide shocks

Voters consuming politically-relevant information for the first time in months or years are likely to possess imprecise prior beliefs, and thus be most susceptible to news because their beliefs are most malleable (e.g. Hirano et al. 2015; Zaller 1992). Conversely, voters consuming news throughout the electoral cycle possess stronger prior beliefs over the issues they regard as important and can better distinguish informative from uninformative signals. These arguments follow, for example, from the career concerns model discussed in Appendix A.1.1 above. They also receive empirical support from Da Silveira and De Mello(2011) and Larreguy, Marshall and Snyder(forthcoming), who find that relatively uneducated voters in Brazil and Mexico respectively respond most to political advertising. Education is widely believed to increase political knowledge by providing the ability, opportunity and motivation to acquire information (Barabas et al. 2014; Delli Carpini and Keeter 1996). Taking higher education as a proxy for the precision of prior beliefs, this subsection examines the extent to which it is the case—at both the individual and aggregate levels—that the least educated voters are most likely to respond to homicide shocks. To test whether less educated voters respond more to performance indicators in the news around elections, I first examine how the effects of short-run homicide shocks on voter beliefs vary by education. Using the ENCUP survey data, I define an education indicator for the 18% of respondents that have completed a university degree (“higher”) education. This is significantly positively correlated with news consumption and political knowledge. The marginal effects of an upcoming local election reported in Table A21 suggest that increased concern about public insecurity and reduced confidence in municipal incumbents are most pronounced among less educated voters. Although

69Unreported results separating neighboring incumbents from the same and different parties, but show no meaningful differences.

A35 Table A20: Effect of pre-election homicide shocks on municipal incumbent electoral outcomes, by neighbor average homicide shock

Incumbent Incumbent Change in Change in party party incumbent incumbent win win party party vote share vote share (1) (2) (3) (4) Homicide shock 0.007 -0.012 -0.000 -0.004 (0.070) (0.069) (0.018) (0.017) Neighbor average homicide shock 0.163** 0.027 (0.082) (0.020) Homicide shock × Neighbor -0.264** -0.045 average homicide shock (0.118) (0.029) Electorate-weighted neighbor 0.152* 0.027 average homicide shock (0.080) (0.019) Homicide shock × Electorate-weighted -0.230* -0.038 neighbor average homicide shock (0.117) (0.028)

Observations 2,739 2,848 163,862 167,076 Unique municipalities 876 904 899 904 Outcome mean 0.55 0.55 -0.05 -0.05 Outcome standard deviation 0.50 0.50 0.14 0.14 Homicide shock mean 0.41 0.41 0.41 0.41 Interaction mean 0.47 0.46 0.47 0.46

A36 Table A21: Effect of upcoming local elections on concern about public insecurity and low conﬁdence in incumbent mayors, by homicide shock and completion of higher education Public insecurity the Low conﬁdence in Change in major problem in the municipal mayor incumbent party the community vote share (1) (2) (3) (4) (5) Upcoming local election -0.021 -0.048* -0.036 0.163 (0.022) (0.025) (0.049) (0.118) Homicide shock -0.006 -0.005 -0.043* -0.013 0.0058 (0.015) (0.013) (0.026) (0.022) (0.0307) Higher education 0.082*** 0.064*** -0.001 0.008 0.0367** (0.021) (0.021) (0.029) (0.024) (0.0165) Upcoming local election 0.107*** 0.096*** 0.143** 0.095 × Homicide shock (0.037) (0.034) (0.063) (0.149) Upcoming local election 0.037 0.045 0.196*** 0.182*** × Higher education (0.033) (0.034) (0.051) (0.058) Homicide shock × Higher education 0.000 0.010 -0.035 -0.037 -0.0443 (0.026) (0.024) (0.040) (0.035) (0.0306) Upcoming local election -0.057 -0.073 -0.494*** -0.487*** × Homicide shock × Higher education (0.054) (0.053) (0.070) (0.075) Local media 0.0027*** (0.0010) Homicide shock × Local media -0.0034** (0.0013) Local media × Higher education -0.0019** (0.0009) Homicide shock × Local media 0.0021 × Higher education (0.0018)

Observations 6,564 6,564 5,916 5,916 29,736 Clusters 196 196 293 293 118 Outcome range {0,1}{0,1}{0,1}{0,1} [-0.63,0.50] Outcome mean 0.13 0.13 0.34 0.34 -0.04 Homicide measure mean 0.47 0.47 0.42 0.42 0.40 Higher education measure mean 0.20 0.20 0.16 0.16 0.50 Upcoming local election mean 0.25 0.25 0.02 0.02 Local media mean 18.69 Survey years without data 2003, 2005 2003, 2005 2003, 2005 2003, 2005

Notes: The specifications in columns (1)-(4) are estimated using the ENCUP data and include survey year fixed effects, and are estimated using OLS; the number of observations differ between columns due to non-responses. The specifications in columns (5) and (6) are estimated using precinct-level electoral returns and includes neighbor group and year fixed effects, and are estimated using OLS; all observations are weighted by the number of registered voters divided by the number of comparison units within each neighbor group. Standard errors clustered by municipality are in parentheses. * denotes p < 0.1, ** denotes p < 0.05, *** denotes p < 0.01.

A37 the triple interaction is not quite statistically significant in the case of public security concerns, the interaction between upcoming local elections and homicide shocks indicate that—summing across coefficients—a pre-election homicide shock only significantly increases the concerns of voters that did not complete upper secondary schooling. I link these individual-level findings to precinct-level voting outcomes by examining whether the effect of local media covering a homicide shock also varies with higher education. I define an indicator for electoral precincts above-median levels of higher education, according to the 2010 Census; i.e. 42% or more of voters with higher education in the relatively urban neighbors sample). Consistent with the survey results in columns (1)-(4), the triple interaction in column (5) of Table A21 suggests, albeit not statistically significantly so, that the electoral sanctioning induced by local media is greater in precincts with low fractions of highly educated voters.

A38