The Unintended Consequences of Conditional Cash Transfer Programs for Violence: Experimental and Survey Evidence from Mexico and the Americas

ABSTRACT: Because conditional cash transfer programs (CCTs) can address the deep roots of violence, many scholars and policymakers have assumed them to be an effective and innocuous tool to take on the issue. I argue that while CCTs may have positive economic effects, they can also trigger social discord, criminal predation, and political conflict and, in doing so, increase violence. To test this claim, I take advantage of the exogenous shock caused by the randomized expansion of Mexico’s flagship CCT, PROGRESA/Oportunidades. I find that the experimental introduction of the program increased rather than decreased violence. Then, I analyze all the data compiled by LAPOP on the issue over the years. I find that, other things constant, Latin Americans are more exposed to violence and insecurity when they participate in CCTs than when they do not. These findings urge us to reconsider the effects of social programs on violence.

CITATION:  Zizumbo-Colunga D. The Unintended Consequences of Conditional Cash Transfer Programs for Violence: Experimental and Survey Evidence from Mexico and the Americas. Latin American Politics and Society. 2023;65(3):47–71. doi:10.1017/lap.2022.67 

Note: What follows is the authors' pre-print version. The final published version can be accessed [HERE]

Conditional Cash Transfer programs (CCTs) have become ubiquitous worldwide attracting the attention of scholars across subfields. While their capacity to benefit the incumbent politically has triggered much debate over the last decade (De La O 2013; Imai, King, and Rivera 2020; Díaz-Cayeros, Estévez, and Magaloni 2016; Araújo 2021), there is a growing consensus that CCTs are effective in incentivizing human capital investments, reduce social inequality, and promote political participation and inclusion (Micheli 2018; Layton, Donaghy, and Rennó 2017; Schober 2019; Morais de Sá e Silva 2017; Jenson and Nagels 2018; Molina-Millán et al. 2019). This evidence has led a growing body of scholars and policymakers to believe that, as they tackle the deep roots of violence, CCTs may have downstream crime and violence-reducing effects (Machado et al. 2018; Lance 2014; Dubois, de Janvry, and Sadoulet 2012; Chioda, De Mello, and Soares 2016; Watson, Guettabi, and Reimer 2020). If confirmed, this consensus would bring positive news to a region going through a vertiginous rise in violence that has left social, economic, and economic order in crisis (Malone 2012; Albarracín and Barnes 2020; Visconti 2020). 

While I do not deny that CCTs could help reduce social conflict in some contexts, in this manuscript, I challenge the consensus by highlighting the mechanisms by which these programs can generate negative externalities that might mute and even revert CCTs’ violence-reducing effects. Then, to investigate the net effect of CCTs, I investigate the case of Mexico. Mexico is an ideal case of study because it was home to the most influential CCT ever implemented in the developing world—the PROGRESA/Oportunidades/PROSPERA program (henceforth PROGRESA) — and recently experienced a rapid rise in violence. I take advantage of an exogenous shock created by a randomized controlled trial implemented during the 1999 expansion of the program, in which 506 marginalized rural localities received two additional years of PROGRESA (Parker and Todd 2017). I find no evidence of the long-term violence-reducing impact of the program. If anything, I find that the villages that adopted the program earlier registered significantly more homicides and violence-related hospitalizations than villages that adopted the program later.

Then, to examine the generalizability of the findings across the continent, I analyze all the individual-level data collected by the AmericasBarometer on CCT participation and insecurity throughout the Americas from 2010 to 2019. The results are consistent. Accounting for other individual and contextual-level confounders, CCT beneficiaries are systematically more likely to report crime and insecurity and, in the countries with the highest murder rates, they are more likely to be afraid of being murdered. 

The findings of this paper contribute to our understanding of social programs by highlighting the difficulty of reducing violence and producing stability solely through anti-poverty interventions. They suggest that, far from generating political stability through specific and diffuse political support (De La O 2013; Layton, Donaghy, and Rennó 2017) social programs can destabilize communities and, in doing so, increase the prevalence of crime and violence (Weintraub 2016; Blattman, Emeriau, and Fiala 2018; Borraz and Munyo 2020). Of course, additional research would be necessary to identify the specific individual, social, and political mechanisms behind this study’s findings. 

1. Violence-Reducing Effects of Cash Transfer Programs

Conditional Cash Transfer Programs (CCTs), involve making direct cash transfers to families to help them fulfill their most urgent needs and incentivize them to make human capital investments. While some note that CCTs can reproduce norms and behavioral patterns that perpetuate gender, social, and economic inequality (Molyneux 2006; Molyneux, Jones, and Samuels 2016; Molyneux and Thomson 2011), research on economic development has found strong evidence that these programs are effective in reducing school dropout rates, food insecurity, and economic deprivation in the short run (Morais de Sá e Silva 2017; Palmeira, Salles-Costa, and Pérez-Escamilla 2020; Parker and Todd 2017) and economic inequality and inter-generational poverty in the long run (Lagarde, Haines, and Palmer 2009; Rudgard 2019; Molina-Millán et al. 2019). While research on the impact of CCTs has focused most frequently on their stated objectives, a new wave of academics and policymakers has argued for the use of cash transfer programs as a socially responsible instrument to address the growing insecurity crises in many countries on the continent. 

Some argue that, because they address the deep-rooted causes of anti-social behavior (Crutchfield and Wadsworth 2003; Enamorado et al. 2016; Fajnzylber, Lederman, and Loayza 2002; Webster and Kingston 2014), in the long run, CCTs can set the stage for peaceful, resilient, and law-abiding communities that can resist internal and external criminal pressures (e.g., U.N. 2015; IACHR 2015). Others, however, do not believe that we need to wait years to reap the violence-reducing benefits associated with cash transfer programs (Chioda, De Mello, and Soares 2016; Camacho and Mejía 2013; Watson, Guettabi, and Reimer 2020). If individuals engage in crime for economic reasons, by subsidizing households’ income CCTs reduce the utility of delinquency and, consequently, have a negative effect on various forms of crime in the short run. Furthermore, by design, CCTs typically reward families and/or individuals for enlisting their children into school. Some authors argue that, since children attending school have no time to engage in delinquency, we do not need to wait years to observe the insecurity-reducing effects of education. Instead, as soon as the school attendance conditionalities of social programs come into effect, we should observe a reduction in various dimensions of crime, what some call the incapacitation effect of education (Jacob and Lefgren 2003; Luallen 2006). 

Several studies have found correlational evidence consistent with the capacity of CCTs to reduce crime and violence. In Brazil, states with a faster adoption rate of the CCT Bolsa Familia have been found to register lower levels of crime (Loureiro 2012). In Mexico and Colombia, municipalities incorporated into PROGRESA and Familias en Acción tend to register lower levels of homicides, injuries, and property crime (Lance 2014; Machado et al. 2018; Rios Salgado and Llano Jaramillo 2021). And in cities like Bogotá and Sao Paolo, the expansion of CCTs has been found to coincide with lower levels of property crime (Chioda, De Mello, and Soares 2016; Camacho and Mejía 2013; Watson, Guettabi, and Reimer 2020).

While these findings are suggestive, they have not been based on experimental methods. They have either been based on cross-provincial and cross-temporal comparisons with limited statistical power or on the statistical analysis of municipal-level data. Moreover, although previous findings can be reconciled, they are frequently contradictory. The same papers that find a negative association between social programs and property crime show a null (Chioda, De Mello, and Soares 2016; Camacho and Mejía 2013; Rios Salgado and Llano Jaramillo 2021; Watson, Guettabi, and Reimer 2020) or positive link between CCTs and armed violence (Weintraub 2016; Zürcher 2017). Thus, it seems critical to theorize about how CCTs can generate negative externalities that may attenuate and even revert their violence-reducing impacts. 

2. Violence-Inducing Effects of Cash Transfer Programs

Just as classic economic, social, and political theory can substantiate an optimistic view of CCTs, there are also theoretical mechanisms that back a link between anti-poverty programs and an increase in crime and violence. It is critical to consider all aspects of the phenomenon to evaluate these programs fairly. 

By incentivizing school enrollment, for example, CCTs can not only incapacitate the youth but also trigger a concentration effect. That is, they can draw students, gangs, and families into the same physical space and, in doing so, increase the likelihood that problems between conflicting groups will be expressed violently. In the United States, Jacob and Lefgren (2003) and Luallen (2006) investigated the impact of exogenous shocks in attendance (teacher in-service days and strikes) on the prevalence of misdemeanors. They have consistently found that, while property crime tends to decline when students are not in session, violent crime tends to increase between thirty and forty-five percent when schools are in session. 

In the medium and long run, concentrating children in schools with insufficient resources to protect youngsters can facilitate rather than difficult criminal recruitment. In Colombia, thousands of children were recruited from poor marginalized schools throughout the civil war (Kirk 1994); in El Salvador, gangs intimidate teachers and principals routinely to recruit students (Martínez-Reyes and Navarro-Pérez 2018; Ramírez 2015). Meanwhile, in Mexico, drug cartels have been found to infiltrate schools, attempting to enlist children as informants, traffickers, and even hitmen (Barrena, Fernández, and Morales 2019; 2011; Salomón 2019; Geremia and Pérez García 2011). 

 Furthermore, even as cash inflows can have positive economic effects, they can also expose beneficiaries to different forms of violence. Most directly, raising citizens’ disposable wealth through cash transfer programs can turn citizens into better loot (Mesquita 2020; Borraz and Munyo 2020). Borraz and Munyo (2020), for instance, evaluated the impact of the 2008 reformulation of Uruguay’s Plan de Equidad on property crime and, contrary to previous studies, found that the increase in the payment to and the number of beneficiaries in the program raised property crime by 1.1 percent. 

Additionally, cash inflows can disrupt familial, communal, and political power equilibria (Adato, Coady, and Ruel 2000; Hays 1982; Villarreal 2002; Díaz-Cayeros, Estévez, and Magaloni 2016). When CCTs do not explicitly incorporate women-empowering components (Molyneux 2006; Molyneux and Thomson 2011) or when they are implemented in contexts of low state capacity, programs that rely on women as their point of contact can generate gender stigmatization and put women in a position in which they can be the target of extractive intra-family violence in the short run (Díaz-Cayeros, Estévez, and Magaloni 2016; Adato, Coady, and Ruel 2000). 

Further, by increasing citizens’ economic autonomy and introducing competing resource-distribution authorities, in the medium-long term CCTs can threaten the political and economic dominance of traditional authorities (Blattman, Emeriau, and Fiala 2018; Díaz-Cayeros, Estévez, and Magaloni 2016). In doing so, they can trigger a reaction that might lead to violence against program operators and citizens willing to vote their conscience (Sesia 2001; Blattman, Emeriau, and Fiala 2018). Finally, since CCTs often target historically marginalized groups, they can trigger some degree of resentment among intolerant majorities and among those who perceive welfare to be unjust (Ellis 2012; MacAuslan and Riemenschneider 2011). To the extent that resentment propels radicalized majorities to exert violence against minorities as a form of social control (de la Roche 1996; King and Wheelock 2007), CCTs can leave beneficiaries exposed to retributive crime and violence.

In addition to their individual-level effects, cash-transfer programs can increase the overall value of localities and, in doing so, trigger political, criminal, and armed territorial competition (Cameron and Shah 2013; Casas 2018; Díaz-Cayeros, Estévez, and Magaloni 2016; Zürcher 2017). Cameron and Shah (2013), for example, examined the impact of the distribution of cash fuel subsidies in Indonesia and found the deployment of the program to be associated with increases in political and ordinary violence, revealing efforts by clientelist and criminal actors to capture the benefits of the program. Similarly, studies about civil war have examined the issue and found that the introduction of direct and governmental aid exacerbates conflict between armed actors (Zürcher 2017). Wood and Molfino (2016) found that in sub-Saharan Africa the introduction of humanitarian aid led to an increase in the number of confrontations between rebel and government forces. For the Philippines, Crost, Felter, and Johnston (2014) found that the distribution of poverty relief amid civil war increased civil casualties. Meanwhile, Weintraub (2016) examined the effect of Colombia’s Familias en Acción and found that municipalities in which the program was implemented registered a significantly faster increase in the number of attacks perpetrated by the FARC. These findings imply that, where political, criminal, or armed actors compete violently to dominate territory, CCTs can expose beneficiaries to higher levels of violence. 

In sum, just as there are reasons to expect CCTs to have a crime and violence-preventing effect, some mechanisms suggest that CCTs can unintendedly increase social, political, and armed conflict. To evaluate the net effect of CCTs on violence, I turn first to the case of Mexico. This country was a pioneer in the design and implementation of CCT programs and has recently seen a vertiginous rise in violence. 

3. Violence and CCTs in Mexico

Over the two decades that followed its transition to democracy, Mexico experienced high volatility in its levels of violence. Although the first political cycle after the advent of democracy was characterized by a steady decline in violence, the following three have been marked by a steep increase. Before former president Felipe Calderón’s presidency (2006), Mexico recorded between ten and fifteen thousand homicides a year (Calderón et al. 2019). By the end of Calderón’s presidency (2012), homicide had doubled, executions had increased tenfold, and the number of missing persons had reached nearly 26,000 (Schedler 2014). Since then, homicides, kidnappings, extortions, and executions have risen in urban and rural communities (Maldonado-Aranda 2012, Calderón et al. 2019). In fact, in 2019, Mexico registered the highest homicide rate in its last twenty years (Angel 2019).

To control rising levels of violence, all federal administrations since 2006 have continued to pursue the policies that many argue gave rise to the problem in the first place (Phillips 2015). They strengthened a prohibitionist approach to drugs, increased cartel decapitation operations, and redoubled their bet for the use of the military as a force to occupy territories. Yet, it must be noted that, since the start of the war on drugs, executives have also highlighted the importance of poverty-reduction programs as a critical strategy to reduce violence. During his presidential campaign, president Andrés Manuel López Obrador (AMLO) summarized his security platform in four words: “becarios sí, sicarios no”.  Also, throughout his presidency, he has attempted to persuade the governments of North and Central America to collaborate in the expansion of the CCTs he has promoted in Mexico, to address the structural economic conditions that create violence and promote migration in the region. 

Although no president before AMLO underlined the violence-reducing potential of poverty-alleviation programs so strongly, all federal administrations have framed PROGRESA as a central part of their long-term security strategy.  Therefore, to estimate the long-term impact of these programs, we need not implement a new CCT and wait for years to see its effects. We can investigate previous CCTs paying special attention on how well they have fared in their efforts to achieve their tangential but stated objective to reduce violence. 

4. The Long-term Effects of PROGRESA on Violence

Mexico’s Education, Health, and Nutrition Program (PROGRESA) was the second iteration of a long history of cash-transfer programs implemented in Mexico since 1988. It was the successor of the National Program of Solidarity PRONASOL (1988 to 1996) and the predecessor of OPORTUNIDADES (2002 to 2014) and PROSPERA (2015–2018). PROGRESA started with a similar objective to PRONASOL, to serve as a stepping stone for low-income families to escape poverty. Meanwhile, it improved over its predecessor by making cash transfers conditional to families enrolling their children in school, complying with an 85% school attendance, preventing their children from repeating a single school year more than two times, and taking their children to regular medical check-ups. During its first year, PROGRESA incorporated 400 thousand families, but by the end of 2016, the program had been taken to more than six million households and had inspired the creation of dozens of similar CCTs around the world (Morais de Sá e Silva 2017; Robles, Rubio, and Stampini 2017).

Although there is a consensus over the positive educational, health, and economic impacts of PROGRESA, evidence of its effect on violence is mixed. Whereas Lance (2014) found a negative association between PROGRESA and homicide rates at a municipal level, qualitative analyses have found a link between PROGRESA and social conflict. Adato et. al. (2010) and Diaz-Cayeros et. al. (2016), for instance, conducted in-depth interviews with citizens in Mexico and found evidence of conflict between beneficiaries and non-beneficiaries, traditional authorities and program managers, and women recipients and their extractive husbands. Similarly, research journalists have investigated the modus operandi of drug cartels in rural areas and have reported how criminal organizations intimidate doctors, teachers, program workers, and beneficiaries to control communities and extract resources from their inhabitants (Proceso 2009). In the words of a member of Mexico’s Council of Farmers and Settlers “[The Cartels] have the list of beneficiaries, they know how much they receive, and they extort and threaten those who do not pay their dues” (interview by MVS Noticias 2010). 

The mixed evidence found by previous studies might be due to methodological and epistemological differences. It may also be due to the inherent limitations of observational and qualitative designs. While PROGRESA has clearer rules than its predecessors, it was  implemented and expanded to localities in which the political, criminal, and structural conditions allow it (Skoufias 2006; Díaz-Cayeros, Estévez, and Magaloni 2016). This situation opens our inferences to observed and unobserved confounders that can introduce selection bias in our inferences. To extract the long-term causal effect of PROGRESA, it would be necessary to identify an exogenous shock that altered the program’s implementation and then follow its effect for years. While finding such a shock is difficult, it is not impossible. 

In the fall of 1997, the International Food Policy Research Institute (IFPRI) started a Randomized Controlled Trial (RCT) in which hundreds of rural-marginalized localities, the lowest statistical unit studied by Mexico’s National Institute of Statistics (INEGI), were randomly assigned to either (a) receiving PROGRESA immediately, or (b) serve as controls for two years. 

The RCT advanced in four stages. In the first stage, researchers selected seven states with high levels of poverty and inequality: Guerrero, Hidalgo, Michoacán, Puebla, Querétaro, San Luis Potosí, and Veracruz. Then, in the second stage, they selected 506 localities within the entire sample. Eligible localities had to score “high” or “very high” in Mexico’s marginalization index, have more than 50 inhabitants, and have at least one school in the area. In the third stage, IFPRI identified poor households within the localities in the trial using a quantitative and qualitative cross-validation process. First, households were ranked by their levels of poverty, using data from the Demographic and Socioeconomic Household Survey (ENCASEH). Then, households were validated as poor by a popular assembly. In the fourth stage, the 506 localities were randomly divided into a treatment (N=320) and a control group (N=186). Households in treatment localities were incorporated into PROGRESA in 1998, and households in the control group were incorporated into the program two years later.  This means that families with children in first through sixth grades started receiving incentives two years earlier and that families with children in eighth and ninth grades only received incentives if they were in the treatment group.  As Figure 1 shows (and Online Appendix A2 confirms), although more localities were assigned to be early PROGRESA adopters, the treatment and control groups tend to be demographically and geographically balanced.

In total, over the course of the trial, the government made transfers to 4,546 households in the 320 treatment localities. It translates to a total of 109,104 monthly cash transfers and—at a rate of 24.6 1999 dollars per transfer—a total of an additional US$2.68 million in 1999. Adjusting for inflation, these numbers imply that PROGRESA distributed an average of 14.7 thousand (2022 inflation-adjusted) dollars per locality and that the government distributed a total of 4.7 million (2022 inflation-adjusted) additional dollars in the treatment group. 

The Mexican government collected numerous variables to measure the economic, educational, and social development of the children and families living in the localities included in the trial (Skoufias 2006; Parker and Todd 2017). Unfortunately, it did not collect information on the levels of crime and violence that occurred in these areas. Thus, the only way to study the shock caused by the trial is to examine data outside of that explicitly collected for the RCT.

Since the 1990s, INEGI has published event-level data on the causes of the deaths registered in the country, in line with the tenth revision of the International Classification of Diseases (ICD-10). The municipal-level identifiers that INEGI has included on this database have allowed scholars to investigate the determinants of violence at this level (e.g. Dell 2015; Enamorado et al. 2016; Lance 2014). Yet, since IFRI randomized PROGRESA at the locality and not the municipal level, an analysis of municipal-level trends in crime cannot help us extract the causal effect of interest. Fortunately, only two years after the end of the trial, INEGI started identifying deaths at the locality level. Thus, while we cannot calculate the number of locality-level homicides immediately before and after the trial, we can estimate the downstream impact of the trial starting two years after its conclusion.

I code as homicides all the deaths caused by armed and unarmed direct violent attacks (X85-Y09 in the ICD-10 list) as well as all the deaths from gunshots of “undetermined intention” (W32-W34 and Y22-Y24) recorded by INEGI. All events recorded extemporaneously were counted in the year in which they occurred.  To analyze the long-term impact of PROGRESA on violence, I examined the first decade of available data. This means the 5,566 locality-years between 2002 and 2012.  I constrained the period under study in this way because it allows me to capture the differences in wealth and school-age children introduced by the program before they erode. 

Homicides emerged as a rare event in the localities under study. In total, authorities registered 37 during the period analyzed. This, may be explained by the fact that localities are in rural areas, authorities filtered out violent states from the trial, or a combination of both.  Because selection occurred before treatment assignment and authorities did not stop recording homicides at any time, selection affected neither the n of our study nor its ability to remove bias from our econometric analyses. Still, to prevent any potential selection bias and increase the efficiency of the estimates, I specify a negative binomial regression model in each locality-year as a function of the following equation.

In this equation, Violence is the locality-year number of homicides, Treated is a dichotomous variable that identifies if the locality was chosen to be an early adopter of PROGRESA. Size' and Violence97', represent two vectors of indicators that identify: (a) the size of the locality in the year t, and (b) the levels of violence in the locality’s municipality before the study (1997).  Θ'State and Φ'Year represent a set of state and year fixed-effects, and e  represents a residual error term clustered at the locality level.

As expected, the model shows that populous localities located in municipalities with higher levels of violence before the trial have a higher probability of registering homicides during the period of analysis (Column 1 in Table 1). More importantly, it shows little evidence in favor of the violence-reducing effect of CCTs. If anything, it suggests that localities experiencing the PROGRESA RCT shock registered a significantly higher number of homicides (p= 0.07) than localities not experiencing this shock. In relative terms, the risk of observing a homicide in localities randomly chosen to start PROGRESA early is 2.16 times larger than the risk in localities chosen to serve as controls. 

While this finding brings initial evidence for the unintended effects of PROGRESA, it is important to acknowledge that not all incidents of violence involve homicides. Fortunately, there is an additional data source that can help us assess further the effects of the program—Mexico’s Automated Hospital Discharge System (SAEH). 

The SAEH—operated by the General Directorate of Health Information (DGIS)—documents each case that is discharged in 98% of Mexico’s public hospitals and clinics (DGIS 2001). The system records patients’ demographic characteristics, date of admission, and condition for which they were treated. Importantly, the SAEH records the cause of all the hospitalizations that involve an external cause (7.21%) according to the ICD-10. This allows us to categorize hospitalizations as non-violence and violence-related hospitalizations (VRH). The latter include hospitalizations caused by aggressions, gunshots, stabbings, or explosive attacks. The former is a residual category.  

While this data is of great value, it has a key limitation. As the randomization of the experiment occurred within municipalities, we can only use the SAEH to obtain a count of the number of VRHs at the locality-year level after 2004 – the first year in which INEGI made public this information. Regardless, evaluating the long-term effect of the exogenous implementation of the trial on non-lethal violence is critical to fully understand the effects of this program. Thus, in line with the previous section, I analyze the first decade of available data on VRHs (2004 and 2014).

Perhaps due to a lack of medical access in rural localities or the inherent rarity of the phenomenon, during the period under analysis (5,566 locality-years), the SAEH recorded only 62 violence-related hospitalizations. Still, this data allows us to produce a secondary test of hypotheses based on cases of violence that do not result in the victim’s death.   

With this objective in mind, I specify a negative-binomial regression model identical to the one presented in equation 1. This time, however, rather than representing the count of homicides, 〖Violence〗_sjt represents the number of VRHs recorded in a locality-year. Its results are presented in Colum 2 of Table 1. Consistent with previous analyses I find no evidence for the violence-reducing effect of PROGRESA. Instead, I find that VRHs are more prevalent in localities that adopted the program early than in localities that adopted the program late. More precisely, I find that, once all factors are held constant, exposure to the PROGRESA trial produced a statistical and substantive increase in the incidence risk of VRH.

All things considered, data on, both, lethal and non-lethal violence suggests that PROGRESA had negative externalities on violence during its first six years of implementation.  How meaningful were these negative externalities? To answer this question, we can use the parameters in Columns 1 and 2 of Table 1 to calculate: (a) the number of events (murders and VRHs) that would have been observed in the years under study had all the localities been assigned to start PROGRESA early, and (b) the number of events that would have been observed had all localities been assigned to wait until the year 2000 to start the program. 

As the panels in Figure 2 show, I estimate that had no locality started PROGRESA until the year 2000, we would have expected to see about 26 homicides and 41 VRHs during the subsequent decade. In contrast, had the entirety of the localities started PROGRESA in 1998, we would expect to see about 55 homicides and 101 VRHs in the same period. Those are 18 more homicides and 23 more VRHs than observed in the data (dotted line), and some 30 additional murders and 44 more VRHs than expected under the opposite counterfactual.  This might seem like a marginal effect but, if we consider that the same year that the trial took place, PROGRESA was introduced in another 43,485 rural-marginalized localities, my findings suggest that PROGRESA could be associated with as many as 2,319 excess homicides and 3,472 excess VRHs. 

Although the rigor of the PROGRESA trial allows me to derive internally valid estimates, it is important to consider three limitations of the results so far. First, as I have mentioned before, since the Mexican government does not make locality-level data on violence available before 2002 (2004 for VRHs), I can only estimate the long-term effect of PROGRESA. While accurate, these estimates are not inconsistent with the program having virtuous short-term effects (Camacho and Mejía 2013; Chioda, De Mello, and Soares 2016). PROGRESA could have reduced crime violence in the first two years in which it was implemented, had null effects over a second phase, and generated socio-political conflict in the long term. Additional information would be necessary to estimate the effect of PROGRESA in its first two years. 

Second, the results presented in this paper are consistent with causal mechanisms related and unrelated to PROGRESA’s stated objectives. As I have discussed before, PROGRESA aimed to increase wealth, human capital, and school attendance (Schultz 2004; Parker and Todd 2017). Yet, it also exposed communities to program operators of questionable repute and opened the opportunity for social and political conflict. Further qualitative and quantitative research would be necessary to distinguish if the increases in violence detected here are a byproduct of rapid economic development, criminal predation, conflicts between central and traditional authorities, or another causal mechanism.

Finally, while the results deriving from the PROGRESA trial have been used to justify the implementation of CCTs across contexts, it is critical to acknowledge that the sample is relatively small (it encompasses only 506 of 189,433) not representative of the country and should be used with care to make strong claims about the impact of PROGRESA—or other programs—in urban areas, in other periods, or in other countries. Further, the findings so far do not necessarily represent a strong rebuttal to the optimistic results found by others in urban areas (Camacho and Mejía 2013; Chioda, De Mello, and Soares 2016; Machado et al. 2018). The violence-inducing effect of PROGRESA could very well be idiosyncratic to the characteristics of the program, the kind of violence experienced by Mexico, the rural context in which the trial was implemented, or a combination of these factors. Additional experimental and observational research would be necessary to investigate whether the findings of this study are consistent with what is observed in other environments. 

To explore the generalizability of the findings presented, in the next section I analyze all the data on social-program participation and violence collected by the Latin American Public Opinion Project (LAPOP). While the observational nature of LAPOP’s data prevents us from deriving strong causal inferences, it provides us with the unique opportunity to investigate the issue at an individual level across a broad number of countries. 

5. Social Program Participation and Violence in the Americas

Since 2004, LAPOP’s flagship project “The AmericasBarometer” has compiled firsthand information on the political culture of the citizens of the Americas. In addition to asking citizens about their democratic attitudes and dispositions, since 2010, the AmericasBarometer has questioned interviewees across the continent about their participation in cash-transfer programs and their exposure to crime and violence.  These data allow us to account for citizens not reporting crime to authorities (Levitt 1998; Skogan 1976) and for the difficulty of inferring individual-level experiences from aggregate data (Seligson 2002).

To investigate the effect of CCT participation on crime and violence, I compare the experiences of interviewees living in households receiving CCT transfers with those not receiving them. All in all, my analysis is based on 141,268 interviews collected in Mexico, Guatemala, El Salvador, Honduras, Nicaragua, Costa Rica, Panama, Colombia, Ecuador, Bolivia, Peru, Paraguay, Chile, Uruguay, Brazil, Venezuela, Argentina, Dominican Republic, Haiti, Jamaica, Guyana, Trinidad y Tobago, Belize, and Suriname. Online Appendix A6 describes the number of interviews in each of the 86 country-waves.

I estimate three regression models. In the first model, I evaluate the effect of social program participation on citizens’ probability of being the victims of a crime (Crime Victim). In the second model, I evaluate the impact of program participation on individuals’ perception of the levels of insecurity in their neighborhood (Neighborhood Insecurity). In the third model, I analyze the effect of CCT participation on citizens’ Fear of Being Murdered. This latter question was only asked to citizens living in the countries with the highest murder rates in the Americas (Mexico, Guatemala, El Salvador, Honduras, Brazil, and Venezuela) and was only included in 2016. Equation 2 shows the general statistical equation specified in each model presented in Table 2.

In Equation 2, Violence represents one of the three dependent variables described before (Crime Victim, Neighborhood Insecurity, Fear of Being Murdered), and CCT Participant represents a dummy variable that indicates whether the interviewee lives in a household participating in a conditional cash transfer program or not. Since the independent variables are not assigned exogenously, it is necessary to account for potential confounders to approximate the net causal effect of interest. The bolded terms in Equation 2 represent six clusters of relevant statistical controls. 

The term λ'Demographic' stands for the demographic variables—age, education, and gender. It is important to control for these variables because CCTs are frequently directed toward women, school-age individuals, and the elderly, and citizens belonging to these groups tend to have different experiences with crime (Singer 2017). The term φ'Economic' represents two relevant economic controls, income level and wealth. Accounting for these factors is critical since, by design, CCTs are systematically directed to families of lower strata, and these families have a different propensity to be involved in crime. To approximate income, I rely on individuals’ self-reported income, and to approximate wealth, I rely on Cordova’s relative wealth measure (Córdova 2009). The term δ'Size' represents the size of the individual’s community, and ξ'Political' represents the two indices included in all waves of the AmericasBarometer that capture two key dimensions of citizens’ political attitudes—Support for the System and Political Tolerance.  I account for the size of individuals’ place of residence because rural and urban areas experience radically different levels of violence and insecurity. I control for political attitudes because—in countries with weak levels of rule-of-law—those supportive of the political system and those willing to condemn dissidents are more likely to become beneficiaries of social programs, more likely to receive public security services, and less likely to suffer or report crime (Layton, Donaghy, and Rennó 2017; Singer 2017). 

In addition to these substantive controls, I also include wave and strata-level fixed effects (Φ'Year',Θ'Subnational Region'). Strata-level fixed effects allow me to account not only for country-level differences but also for geographical variations within countries (e.g., distinguishing between Northern and Southern Mexico).  Table 2 shows the results of the three models mentioned above. When the dependent variable is dichotomous (Crime Victim), I specify a logistic regression model. When the dependent variable is on a 1 to 5 Likert scale (Neighborhood Insecurity and Fear of Being Murdered), I rescaled it to run from 0 to 100 and specified a multivariate OLS model. 

The results in Table 2 are clear. Holding individuals’ wealth, income, gender, age, education, support for the system, and political tolerance constant, CCT beneficiaries are significantly more likely to be victims of crime, report their neighborhoods as being more insecure, and be more fearful of being murdered. Focusing on the first of the three findings, the odds of an average Latin-American of becoming the victim of a crime is 5.46% higher if he/she is a program participant than if he/she is not. This suggests that expanding social programs to an additional 10,000 households could lead to as many as 107 additional crimes a year. In relative terms, this effect is equivalent to 45.53% of the effect of gender, 37.37% of the effect of income, and 20.84% of the effect of living in an urban area.

While these estimates are in line with experimental data and are robust to controlling for pre-existent levels of neighborhood and municipal-level insecurity (see Online Appendix A8) they should also be taken with care as they cannot fully account for the bidirectional relation between the variables of interest.  Additional cross-national experimentation would be necessary to fully establish the causal link of interest. While such an ambitious exercise may be undertaken, LAPOP’s data suggests that the findings in the first section of the manuscript should not be dismissed as a fluke emerging from the uniqueness of the context in which the PROGRESA trial took place.  

6. Conclusion

Because of their economic and political importance, Conditional Cash Transfer Programs (CCTs) have attracted the attention of economists and political scientists over the last two decades. While academics and policymakers have suggested that these programs could be an effective policy tool to prevent and reduce crime and violence, empirical and journalistic evidence suggests that, in contexts of low rule of law, CCTs can expose beneficiaries to social, criminal, and political violence. In this paper, I have reviewed the potential impacts of CCTs, paying particular attention to how CCT programs could have an unexpected and unintended violence-inducing effect. 

To assess empirically the net effect of cash-transfer programs, I looked at the case of Mexico. This country played a leading role in the design and implementation of CCTs during the 2000s, has become one of the most violent countries in the region, and has recently promoted the use of cash-transfer programs as a strategy to reduce violence. I took advantage of an exogenous shock created by the 1998–2000 experimental expansion of Mexico’s PROGRESA to estimate the causal long-term impact of the program on locality-level homicides and violence-related hospitalizations. I found little support for the optimistic view of CCTs and support for the idea that the introduction of PROGRESA caused an unintended increase in violence. Localities exposed to PROGRESA for two additional years recorded significantly more violence in the decade that followed the study. While this data brings valuable insights to our understanding of the impact of CCTs it is limited in its broadness. Thus, to assess the generalizability of these findings, I analyzed, arguably, the broadest comparable database on CCT participation and violence—the AmericasBarometer. The data compiled across twenty-five countries between 2012 and 2016 brings little support for the rosy view of CCTs and, on the contrary, shows that—once other factors are accounted for—beneficiaries are more likely to become victims of crime, perceive their neighborhood to be insecure, and be fearful of being murdered. 

These findings bring support to a growing literature critical of CCTs. Just as some anti-poverty programs can fail to empower women, in fact consolidating traditional gender roles (Molyneux, Jones, and Samuels 2016), this paper’s results suggest that, when CCTs are not accompanied by strategies to reduce crime and violence, they generate the conditions and incentives in which these phenomena can become exacerbated (Borraz and Munyo 2020). 

Moreover, my results have implications for our understanding of the political consequences of CCTs. Others, have found that, although redistributive cash-transfer programs are deployed with a political objective in mind (Díaz-Cayeros, Estévez, and Magaloni 2016; Penfold-Becerra 2007; González and Mamone 2015), they fail to deliver the political benefits expected (Imai, King, and Rivera 2020), are seldom able to distract citizens from corruption and economic underperformance (Pavão 2016), can generate contention among partisans (Corrêa and Cheibub 2016), and can even lead to the growth of the opposition in the long run (Blattman, Emeriau, and Fiala 2018). My findings suggest that—to the extent that the context allows them to do so—political actors may use violence to secure the electoral gains they cannot obtain through redistribution, to resolve intra-partisan conflict, or to contain the losses that a wealthier and more independent electorate entails. Of course, additional qualitative and quantitative research would be necessary to deepen our understanding of how the expansion of CCTs can intensify political and social conflict at the local level.

An open question that is not answered in this paper is whether the violence-inducing effect estimated here varies across social programs. While further research is needed in this area, it is important to point out that this heterogeneous impact is likely to be contingent on the mechanisms underlying the violence-inducing effects of CCTs and the very nature of the programs. If violence emerges from political elites’ frustration with their incapacity to control a wealthier and more independent electorate, the negative effects of social programs might be stronger where they are better shielded against clientelist manipulation. If the effects are driven by the medium-term predation of the additional human and economic capital introduced to communities (Kaufman and Trejo 1997; Díaz-Cayeros 2008), the violence-inducing effects of social program might be even stronger in places where elites can distribute cash more privately and discretionally. 

More theoretical and empirical research would be necessary to identify the institutional and contextual factors that moderate the effects of cash-transfer programs. Rather than bringing closure to this debate, this paper seeks to inspire others to incorporate the unintended effects of social programs into our models of development policy and our understanding of the emergence of violence.

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Endnotes

 [1] “Yes to scholarship recipients, no to hitmen” [author’s translation].

[2] In Online Appendix A1 I show how not only AMLO but also other presidential candidates—as well as the national development plan—consistently see social programs as part of the strategic actions implemented to prevent violence.

[3] Data available at https://evaluacion.prospera.gob.mx

[4] When PROGRESA was introduced in control localities, families with children in eighth and ninth grades were no longer eligible.

[5] Counting deaths by gunshots of “undetermined intention” as homicides is important because, during conflict, it is difficult for government officials to identify the causes of murders.

[6] The period analyzed includes a total of 11 years. As Online Appendix A4 shows, the results become violence-inducing after 2005 (5 years after the trial) and remain significant between 2005 and 2016 (the last year under analysis), independent of the period under analysis.

[7] Skoufias (2006) notes that, “localities in the states of Campeche, Chiapas, Chihuahua, Coahuila, Guanajuato, Oaxaca were screened out of the trial for a variety of socioeconomic reasons including the possibility of having security problems for the enumerators” (p. 28).

[8] I specify these variables as categorical to account for non-linearities within them. Since INEGI does not identify murders at the locality, it is the only way to account for ex-ante levels of violence. Yet, as Online Appendix A3 shows, the results are robust to removing all substantive controls (population and homicides).

[9] The SAEH database contains between 1.79 and 2.9 million records each year. I classify an external cause to be violence-related when it involves the following ICD-10 codes: W32–W34, X85–Y09, Y22, Y23, Y24, and Y36.

[10] Especially if one considers that, by 2004, all localities had been included in PROGRESA.

[11] As Online Appendix A5 shows, the results are robust to conducting a clustered randomized inference test. In total, I find that under re-randomization, the results presented here replicate in fewer than three of every thousand iterations.

[12] I rounded decimals to their nearest whole number for simplicity. The locality-year AMTE is 0.0053 (0.0029) for homicides and 0.00798 (0.00333) for VRHs.

[13] This extrapolation should be taken with a grain of salt, as a proper extrapolation would require incorporating sampling and propagation error.

[14] In 2010 and 2012, LAPOP asked citizens whether they received monthly assistance in the form of money or products from the government. In the remaining years—including half of the sample in 2012—it asked interviewees whether someone in the interviewee’s household was a beneficiary of the country’s main Conditional Cash Transfer Program. In Online Appendix A6, I list the questions analyzed in this study.

[15] In Online Appendix A6, I describe the questions that compose both indexes.

[16] All analyses were conducted using the STATA 15.1 svy module.

[17] Online Appendix A7 shows that the violence-inducing impact of CCTs extends to considering moving out of fear of crime, limiting places of recreation, perceptions that shootings are a problem, and perceptions that assaults are a problem. Online Appendix A8 shows that the results are robust to controlling for perceptions of neighborhood insecurity, the number of interviewees victimized in the municipality, and government-reported municipal homicide rates. Finally, while omitted-variable bias influences the results for crime victimization and fear of homicide, the results for perceptions of insecurity remain unchanged when all controls are omitted (see Online Appendix A9).