Inquisitorial Criminal Justice in Latin America

In most ancient, medieval, and early modern societies, judicial torture was legal and formally regulated. In the Middle Ages, the torturer was employed by the King or the Inquisition. His function was to obtain confessions from suspects and heretics. Such confessions served as the “queen of evidence” (Regina probationem), which led to the systematic use of torture as a method of prosecution (Peters Reference Peters1996; Ruthven Reference Ruthven1978).

Beginning with England in 1700, most European nations abolished judicial torture by 1850 (Pinker Reference Pinker2011). Criminal justice was imbued with rationalistic ideas, including that torturing people to extract confessions was an ineffective method of discovering the truth. Instead, the notion that trials should be based on evidence was gradually embraced. Procedural reforms played a critical role to reduce torture in Continental Europe. In 1808, Napoleon introduced his Code d’instruction criminelle, which translated a number of ideas from the English model of criminal procedure to civil law (Langer Reference Langer2007). Its ideas spread across Europe, including Spain. When Latin American countries became independent, they rejected the more liberal European codes and kept the inquisitorial system that had prevailed in the Portuguese and Spanish Americas. The main characteristics of these inquisitorial codes are that the backbone of the criminal process is a written dossier (expediente) that the police and investigating judge compile with all procedural activity; pretrial investigations remain written and secret; the verdict phase is also predominantly written and lacks a jury; and the judge investigates, prosecutes, and adjudicates (Langer Reference Langer2007).

Because of their strong reliance on confessions and weak procedural standards, inquisitorial criminal justice systems expand opportunities for the police to torture. In their empirical cross-sectional study of torture, Conrad and Moore (Reference Conrad and Moore2010) use a dummy variable for civil law countries as a proxy for inquisitorial criminal justice procedures and find that this increases torture. The problem with their approach is that, as the case of Latin America makes explicit, many civil law countries have actually abandoned the inquisitorial model. Hence, to our knowledge, there is no systematic empirical evidence that the inquisitorial model is associated with more torture.

During the last two decades, a major institutional transformation took place as many Latin American countries reformed their inquisitorial criminal justice procedures. The dates of these implementations were as follows: Argentina (1991), Guatemala (1994), El Salvador (1998), Costa Rica (1998), Venezuela (1999), Chile (2000), Paraguay (2000), Ecuador (2001), Bolivia (2001), Honduras (2002), Nicaragua (2001), Dominican Republic (2004), Colombia (2005), Peru (2006), and Mexico (2008) (Biebesheimer and Payne Reference Biebesheimer and Mark Payne2001; Langer Reference Langer2007; Rodrigo de la Barra Cousino Reference Rodrigo de la Barra Cousino1998; Ungar Reference Ungar2002). With a few exceptions, in most of these cases, reforms were adopted years after democratic transitions, which means that democracy in most cases was born with limited human rights protections. Although the new criminal justice procedures implemented in the region vary, most provide for an oral hearing and an adversarial process. Additionally, these new procedures expand judicial oversight over the investigation, institute legal checks on police actions, and add more procedural protections for defendants.

Despite the importance of the reforms, there are basically no empirical investigations about their impact. To our knowledge, the only exception is Kronick and Hausman (Reference Kronick and Hausman2019), who demonstrate that the reforms reduced the number of arrests in Columbia and Venezuela and increased extrajudicial killings in the latter case. Here, we explore how the reforms shaped torture in criminal prosecution in Mexico, the country that has taken longest to adopt them.

The Case of Mexico

The scholarly literature argues that autocrats use repression, including torture, to extract information about potential conspiracies, to dissuade opponents, and to punish acts of dissent (Blaydes Reference Blaydes2018; Davenport and Inman Reference Davenport and Inman2012; Svolik Reference Svolik2012; Wantchekon and Healy Reference Wantchekon and Healy1999). Our paper examines a case of widespread torture that the police and public prosecutors would use in common criminal trials. This does not deny that Mexico’s autocratic regime resorted to torture to repress political dissidents. For example, there is ample evidence that during the Dirty War (1965–1982), torture was used as a way of pursuing political enemies (Aviña Reference Aviña, Herrera and Cedillo2012; Castellanos Reference Castellanos2007; González Villarreal Reference Villarreal and Roberto2014). But torture was not always mandated by the top political leadership. It emerged as the modus operandi in criminal prosecution as coercive institutions liberally used it to extract confessions in criminal trials.

During the autocratic period, courts gave confessions full evidentiary value regardless of how they were obtained or whether the suspect had been given access to a lawyer. Magaloni, Magaloni, and Razu (Reference Magaloni, Magaloni and Razu2018) cite several jurisprudential theses that illustrate this problem. The Supreme Court in this period allowed as admissible confessions even if there was evidence of physical mistreatment or prolonged detention, ignored protests about denials of access to counsel, and placed high probative value on confessions made to the police even if the defendant tried to recant his statements before a judge. In short, the judiciary created a permission structure for police to violate fundamental rights in the administration of justice. Naturally, prosecutors and police came to see coerced confessions, the intimidation of witnesses, and the fabrication of evidence as attractive options for closing cases.

Judicial Checks on Prosecutions

Our theoretical discussion highlights judicial checks on prosecutors and police as one of the main reasons why the criminal justice reforms restrain torture. The reform introduced new protections like the explicit prohibition of torture and the fact that confessions are inadmissible in court unless they are extracted in the presence of a defense attorney. To be effective, these legal prohibitions require judicial willingness to enforce them. Thanks to the criminal justice reform, for the first time the Mexican judiciary would have an explicit constitutional mandate to impose checks on prosecutors and police. A critical question is the extent to which courts actually have begun to impose these controls.

In order to shed light on this mechanism, we use a structural topic model trained on a corpus of 2,078 Mexican jurisprudential theses. A topic model presents text generation as a hierarchical model in which an author draws a topic at random, then draws a word at random from a distribution over words that is specific to that topic; the model infers topics in a document conditional on the distribution of words in that document and the co-occurrence of words across documents (Blei Reference Blei2012; Blei, Ng, and Jordan Reference Blei, Ng and Jordan2003). Here, we present results from a model with five topics.Footnote ⁴ The texts were scraped from the website of the Mexican Supreme Court covering the period from 1988Footnote ⁵ to early 2019 and are those that were classified by the Court as relating to criminal law. Decisions were classified based on whether a given topic was a plurality of the estimates for the thesis. We then plot the proportions of each year’s decisions classified under each topic against the year the decision was published in Figure 1.

Note: This figure shows Supreme Court decisions relating to criminal law classified by a structural topic model. Lines are Lowess estimates for the overall proportion of each topic in each year. The vertical line marks 2008. Topic 4 corresponds to issues related to human rights and criminal procedure.

Figure 1. Jurisprudential Theses on Criminal Law, 1988–2019

Note: The figure shows the incidence of turf wars at the municipality level, defined as increases in homicides of more than three standard deviations from the municipality’s historic mean. Homicide data since 1990 is for males ages 18 to 39 and comes from SINAIS. We draw from Robles (Reference Robles2016) to calculate these turf wars.

Figure 2. Turf Wars from 2013 to 2018

Topic 4Footnote ⁶ in this model is closely tied to concerns about basic human and procedural rights, international law, and torture. This topic begins as the least common class of decisions in 1990 and then starts steadily increasing around 2008 when the reform process began. We note that although the reform was not implemented in the states until after 2014, the corpus of law was incorporated into the constitution in 2008, which opened the door for the Supreme Court to begin to interpret it.

Technically, most cases involving violations of due process rights and allegations of torture arrive in federal courts through Amparo trials (a form of habeas corpus). By raising constitutionality issues, cases could reach the Supreme Court even before the implementation of the reform at the local level. After implementation, it stands to reason that more cases related to violations of due process would begin to be heard before lower level courts, whose decisions can be challenged in Collegiate Tribunals. The Supreme Court has a right to take these cases. It goes beyond the scope of this paper to document how lower level courts are enforcing the new legal corpus, but we believe that variation across states in judicial capacityFootnote ⁷ and willingness to enforce the legal corpus might help explain why the reform is more effective in some states than others. We leave this question for further research.

To illustrate the importance of judicial checks for restraining torture, we discuss two highly visible rulings. The first involves a 2013 decision to release twelve people serving prison terms for a 1997 massacre in the community of Acteal, Chiapas, in which 45 victims were killed. The Court argued that the evidence presented by the Attorney General’s Office was illicit because he used “forged evidence and coerced testimonies”—the main evidence presented against the accused and by which they were all convicted. Another historic decision came in 2018 from the First Collegiate Tribunal of the 19th Circuit against the Attorney General’s Office for its illicit investigative tactics regarding the disappearance in 2014 of 43 students from the rural college of Ayotzinapa. The Tribunal upheld the decision of a lower-level court that ruled in favor of four imprisoned witnesses who said they were tortured by the authorities as part of the federal investigation. Moreover, the tribunal condemned the Attorney General for having used torture as one of the components of a fabricated case.

Exploratory interviews we collected with police officers in Guadalajara, Monterrey, and Mexico City between the fall of 2017 and first six months of 2018, which we discuss in Section 8 of the Online Appendix, reveal that the expectation that judges will release suspects if police violate due process is a major force driving changes in police behavior, also contributing to change in the way police corporations reward officers. Monetary bonuses for the number of arrests or “solved murders per month,” which have been common practices, generate incentives for police to torture and, as some of our interviewees revealed to us, these incentives are “no longer compatible with the criminal justice system.”

Implementation of the Reform

The staggered implementation of the reform is outlined in Table 1. The dates are the unique dates on which the reform was implemented within that state. States with only one date imply that the reform was implemented across the state all at once, while those with multiple dates imply staggered implementation across judicial districts.

Table 1. Reform Implementation Dates Examined

Note: States with only one date imply that the reform was implemented across the state all at once, while those with multiple dates imply staggered implementation across judicial districts. Asterisks refer to states that implemented the reform by category of crime.

There were three ways by which states updated their systems. States (a) created a timetable whereby the reform would take effect in specific geographic units (judicial districts or the entire state) on a certain date, (b) created a timetable whereby the reform would begin covering certain classes of crimes on a given date, or (c) chose some combination of the two. Asterisks indicate jurisdictions that implemented the reform following methods (b) or (c). We obtained the dates of implementation by state through the Supreme Court’s website and state records.

As noted by Shirk (Reference Shirk2010), the scope and scale of change contemplated under the 2008 judicial reforms were enormous. Existing legal codes and procedures needed to be revised both at the federal and state levels; courtrooms needed to be remodeled and outfitted with recording equipment; and judges, court staff, police, and lawyers needed to be retrained to operate under the new system (234). There is likely a great deal of heterogeneity in the way states have adjusted to the reform. On one hand, states might rely more on coerced confessions due to organizational weaknesses and a lack of capacity to investigate crimes, which might partly be driven by absence of adequate personnel, protocols, training, and funding. Institutional corruption might also be driving lack of capacity to investigate crime. In many states, local police are regularly effectively captured by OCGs. Whether they are captured or not might be an important factor in whether they torture and whom they victimize. Moreover, as argued above, local courts’ independence and capacity also matter. Section 4.6 of the Online Appendix presents evidence that bureaucratic and judicial capacities are associated with less torture. In the main body of this paper, we will hold state-level characteristics constant, seeking to identify the causal effects of the abandonment of inquisitorial criminal procedures on torture. We test the following hypothesis:

Abuse in the Mexican Criminal Justice System

Table 2 reports the different forms of abuse prisoners experienced. The table distinguishes between reported abuses before the prisoner arrived at the MP and abuses at the MP. It reports the percentage of prisoners experiencing some kind of abuse and the total numbers in parentheses. Notably, violent forms of institutionalized torture are alarmingly common. These forms of institutionalized torture are slightly more common before the suspect arrives at the MP, and they probably take place either in a clandestine detention center or at the police headquarters. Many prisoners report other kinds of abuses, including being held incommunicado, stripped, restrained or tied, or blindfolded. The data also suggest many prisoners are subject to abuses both before and after arriving at the MP.

Table 2. Abuses Reported by Prisoners

Note: This table shows reported rates of different kinds of abuses for the entire sample of state and federal prisoners. We show the total number of prisoners in each category in parentheses.

Table 3 classifies abuses into the three categories that will be used for the empirical analyses: brute force, institutionalized torture, and threats. The table also includes basic descriptive statistics that will be relevant for our analysis. The descriptive statistics reveal that abuse is endemic throughout social and demographic subgroups of the data. The data reveal that municipal and ministerial local police forces perform the overwhelming majority of the arrests. As expected, there is a significantly higher incidence of torture for prisoners detained in federal prisons and among those who were detained by the military and federal police. These data reinforce the findings in Magaloni, Magaloni, and Razu (Reference Magaloni, Magaloni and Razu2018), which show that the armed forces are significantly more prone to engage in torture. Although the army, in theory, has better training, better weapons, and may be less corrupt, they deal with more violent threats and engage in more armed combat against OCGs than local police forces do. Moreover, their specialized training, equipment, and culture makes them more prone to use extrajudicial force (Flores-Macías and Zarkin Reference Flores-Macías and Zarkin2019; Pérez Correa, Silva, and Rodrigo Gutiérrez Reference Correa, Catalina and Gutiérrez2015).

Table 3. Covariates of Torture

Note: The rows show the percentage of prisoners in each of the subgroups experiencing abuse. Columns 4–5 report the percentage and total number falling in each category.

Those accused of theft are equally or more likely to be tortured and brutalized than those accused of homicide. These data reveal that the Mexican inquisitorial criminal justice system punished poverty, detaining and torturing thousands of people for petty theft. There is a higher incidence of torture among those accused of kidnapping, possession of illegal weapons, extortion, and drugs commerce. The last rows of the table show that 66% of respondents reported having been subject to brute force, 54% to torture, and 65% to threats.

In terms of how truthful prisoners’ responses might be, it is important to mention that although the majority of respondents had been convicted, those who were in prison waiting for a sentence could have assumed that their answers were consequential for their sentences and might possess more incentives to lie. Table 4 shows the conviction status of the prison population: around 68% had been convicted at the time of the survey, 29% were waiting for a sentence, and 2% were “partially” sentenced. The table also shows the percentage of individuals in each group who reported abuses. Propensities to report abuse are lower among convicted prisoners than among those who had not been convicted, which suggests that the latter group might be giving systematically different responses. The “partially sentenced” group shows a significantly higher propensity to report abuses. We deal with this in the Appendix by matching on sentencing status.

Table 4. Conviction Status and Reported Abuses

Note: Rows 1–3 show reported rates of abuse by conviction status. Row 4 shows total number of prisoners reporting each kind of abuse. Column 4 shows the total number of prisoners in each conviction category.

Trends

Our dependent variables correspond to the three forms of abuse defined above. Each is a binary indicator for whether a respondent reported that kind of abuse. We will use OLS regressions because our models include geographic and time fixed effects, which generate problems in logistic regressions. In Table A3 of the Online Appendix, we present our main models using logits and all of our results hold. To explore time trends, we run the following model:

(1)$$ {y}_{ist}=\alpha +{\lambda}_s+{\gamma}_t+{\epsilon}_{ist},\kern1.00em $$

where $$ {y}_{ist} $$ is a dichotomous indicator that takes the value of 1 if prisoner $$ i $$ reports any type of abuse that corresponds to our definition of institutionalized torture, brute force, or threats. The model uses fixed effects for the year and state where the prisoner was detained ($$ {\lambda}_s $$ and $$ {\gamma}_t $$, respectively).

We plot predicted rates of abuses for all prisoners by their year of arrest. As shown in Figure 3, institutionalized torture, brute force, and threats seem to decline gradually until 2006. After that, these abuses increase precipitously until about 2012. These increases coincide with the onset of the Drug War. Abuses then decline with the end of the Calderón presidency. The implementation of criminal justice reform after 2014 appears to accelerate the rate of decline. From these time trends we, of course, cannot infer the causal effects of the Drug War or the reforms. The sections below offer a series of statistical tests to demonstrate causal effects.

Note: The figure shows predicted rates of different forms of abuse by the year of arrest and their 95% confidence intervals from three OLS regressions. All models include year and state fixed effects. The first vertical solid line is the year the PRI lost the presidency (2000). The second vertical solid line indicates the onset of the Drug War (2007). The vertical dashed line is when states began to implement the reform (2014).

Figure 3. Year of Arrest and Types of Abuse

Effects of the Reform

To estimate the effects of the reform, we merged the survey data with the dataset of reform dates described above. To assign prisoners to the treatment, we focus on states that implemented the reform in specific geographic units (judicial districts or the entire state) on a certain date, which are the majority of states.Footnote ¹⁰ For states that have multiple implementation dates, each corresponding to defined regions or judicial districts within the state, we examine the municipality where the arrest took place and identify whether that arrest took place before or after the implementation of the reform in that municipality. Any individual arrested on or after the implementation date in a given municipality is considered to have been arrested under the new system.

Table 5 classifies the data in the pre-reform and post-reform periods. The comparison of the entire pre- and post-reform periods shows a dramatic decline in the occurrence of these abuses. Estimating the causal effect of the criminal justice reform on torture is complicated by the fact that unobserved factors may simultaneously lead to the implementation of the reform and affect torture. Our strategy for overcoming this identification challenge relies on a difference-in-difference statistical approach where first, we use judicial district, municipal, or state fixed effects to hold constant time-invariant characteristics of the local police organizations, judges, and authorities. Second, we use fixed effects for the year of the arrest. These are essential to capture national policy effects (e.g., the onset of the Drug War, alternation of political power in office and electoral competition, etc.).

Table 5. Abuses Before and After the Criminal Justice Reform

Note: Percentage of prisoners experiencing each form of abuse in the pre- and post-reform periods. Row 4 indicates the total number of prisoners arrested in each of the periods. The total number of prisoners drops with respect to those reported in Tables 1–3 because we only include prisoners from states that implemented the reform using the geographic criteria.

The model specification is as follows:

(2)$$ {\displaystyle \begin{array}{ccc}{y}_{ist}=\alpha +{\beta}_1{T}_i+\sum_k{\delta}_k{X}_{ik}+{\lambda}_s+{\gamma}_t+{\epsilon}_{ij},& & \end{array}} $$

where $$ y $$ is a dichotomous indicator that takes the value of 1 if prisoner $$ i $$ reports any type of abuse that corresponds to our definition of institutionalized torture, brute force, or threats, and $$ {T}_i $$ is an indicator variable for treatment. The model also includes$$ k $$ individual covariates as well as judicial district and time fixed effects ($$ {\lambda}_s $$ and $$ {\gamma}_t $$, respectively). In terms of individual-level controls, we include age at arrest, gender, education, indigenous language, and income.Footnote ¹¹

Results of the regression models are provided in Table 6. We find consistent effects of the reform, in the range of 4 to 8 percentage point reductions of different forms of police brutality, depending on type of abuse and model specification. Models 1 to 3 use state fixed effects, models 4 to 6 use judicial district fixed effects, and models 7 to 9 use fixed effects at the municipal level.Footnote ¹² In all specifications, we find statistically significant negative effects of the reform.

Table 6. Effects of Criminal Justice Reform: OLS Models

Note: Estimated coefficients for the criminal justice reform from OLS regressions. All models include socioeconomic characteristics and year fixed effects. Standard errors (in parentheses) are clustered by judicial district. ***p < 0.001, **p < 0.01, *p < 0.05, ⁺p < 0.10.

In section 4.5 of the Online Appendix, we present evidence of pre-treatment parallel trends. Following Autor (Reference Autor2003) and Angrist and Pischke (Reference Angrist and Pischke2009), we estimate models with monthly leads and lags of the treatment. The models show little evidence of a prior effect, with leads near zero. Additionally, we estimate a stricter model that relaxes the assumption of a common trend by estimating models with unit-specific time trends. These latter models were estimated using state, judicial district, and municipal level time trends. We also estimate this using months, rather than years, as the temporal unit of analysis. We further estimate our main results with state-year fixed effects to avoid assuming linear trends in the data when controlling for changes over time. All 42 models considered in that section of the Online Appendix still pick up the effect of the reform, dramatically bolstering our confidence in our identification strategy.

Confounding Factors

A possible objection to our results is that the decline in torture could result from the fact that, after the reform, police might be arresting fewer criminals for less serious crimes and these persons might be less likely to be tortured. As part of the presumption of innocence, the 2008 reforms seek to limit the use of pretrial detention. Under the new laws, pretrial detention is intended to apply only in cases of violent or serious crimes and for suspects who are considered a flight risk or a danger to society. Although many argue that the law gives too much leeway for interpretation, one of the implications of this law is that we should observe fewer detentions for less serious crimes.

In Figure 4, we present coefficients from OLS models for monthly arrests by crime before and after the reform according to crime. Our sample has fewer arrests for theft after the reform and slightly more prisoners arrested for kidnapping. We also inquire whether the composition of our sample by arresting authority changes with the reform. As shown in Figure 4, our sample’s proportion of arrests by the armed forces, federal, and state police do not change with the reform. We have a slight increase in the proportion of prisoners in our sample arrested by the ministerial police and a decrease in arrests by the municipal police.

Note: The figure shows predicted arrests by crime and arresting authority for the 12 months before and after the implementation of the reform and their 95% confidence intervals from nine OLS regressions. Full tables of coefficients are shown in Section 4.7 of the Online Appendix. Errors are clustered at the judicial district level. The vertical line is the implementation of the reform.

Figure 4. Proportion of Arrests around Reform by Crime and Coercive Institution

The fact that the post-reform sample sees declines in arrests for theft and arrests by municipal police poses a problem for our analysis. Table 3 shows that individuals arrested for theft are a substantial portion of our sample and are actually tortured at high rates, though they are far from the most likely to be victims. Moreover, municipal police torture at lower rates than other authorities do and although this would work against our argument that the reform reduces torture, we need to account for this potential confounding factor as well. To deal with this problem we cannot simply run a regression controlling for these covariates, as we have just shown that some of these variables are themselves affected by the treatment of interest. Consequently, we follow the procedure set out in Imai et al. (Reference Imai, Keele, Tingle and Yamamoto2011) and its implementation in Imai and Yamamoto (Reference Imai and Yamamoto2013) to explore whether and how these factors mediate the effect of the reform in reducing torture. They propose a method to estimate both the average causal mediation effect, or the effect of the mediator, and the average direct effect of the treatment. Briefly, we estimate two equations—one for the moderator (M _ist) and one for the dependent variable (Y _ist):

(3)$$ {\displaystyle \begin{array}{ccc}{M}_{ist}={\alpha}_1+\tau {T}_{ist}+{\lambda}_t+{\gamma}_s+{\epsilon}_{ist},& & \end{array}} $$

and

(4)$$ {\displaystyle \begin{array}{ccc}{Y}_{ist}={\alpha}_2+\tau {T}_{ist}+\beta {M}_{ist}+{\lambda}_t+{\gamma}_s+{\epsilon}_{ist},& & \end{array}} $$

where α is an intercept, τ is the coefficient on the treatment, β is the effect of the moderator, and $$ \lambda $$ and $$ \gamma $$ are year and judicial district effects, respectively. Their method then generates predictions for the mediator under treatment and control, and it then uses these values to predict missing values in a potential outcomes model that includes the mediator and the treatment. Their method uses bootstrapping to estimate uncertainty.

The purpose of this exercise is not to identify the causal pathway but rather to see whether, while being generous to the hypothesis that our results are being driven by these imbalances in posttreatment covariates, we find evidence that the mediator explains our effect. We run this for each of our dependent variables twice—once using arrests for theft as the moderator and again using arrests by the municipal police. The results from this test are reported in Table 7; the direct effect remains when accounting for the mediation, which appears to be quite small in substantive terms across all the models.

Table 7. Mediators

Note: Results from a mediation analysis testing whether the pre- and post- treatment imbalance in arrests by the municipal police and arrests for theft is driving our results. All models include socioeconomic characteristics. Bootstrapped standard errors clustered by judicial district are reported in parentheses. ***p < 0.001, **p < 0.01, *p < 0.05, ⁺p < 0.10.

Robustness tests

In Table 8 we present a series of robustness tests. First, we test whether there is a detectable effect of jurisdictions anticipating the reform’s implementation. Each state legislature published official declarations announcing the timetable for the reform’s implementation in 2014. We constructed a variable to indicate the period after the reform’s timetable was first announced but before the reform was actually implemented. This means we then have a sample divided into the pre-reform but pre-announcement era, the post-announcement but pre-reform era, and the reform era. When we ran these models, we did not find anticipation effects.Footnote ¹³

Table 8. Placebo Tests for the Criminal Justice Reform

Note: Entries are estimated coefficients from OLS regressions for placebo tests that move the start dates of the reform two, three, and four years before the actual dates. All models include socioeconomic characteristics. Standard errors (in parentheses) are clustered at the judicial district level. ***p < 0.001, **p < 0.01, *p < 0.05, ⁺p < 0.10.

We implemented additional placebo tests in which we artificially move the date of the implementation of the reform beyond our “announcement period” to two, three, and four years prior to the actual implementation. We repeat the specifications from the main model analyzing these “faked” reforms truncated at the date of the real reform. We report the coefficients on the artificial reform variable in Table 8 and find no significant effects across any of the models.

Lastly, in section 4.3 of the Online Appendix, we rerun our tests and use coarsened exact matching on crime, arresting authorities, and sentencing status to ensure balance in covariates that may be unbalanced in the pre- and post-reform periods and related to the outcome variables. Our results hold after we match on these variables. The Online Appendix also shows that the results are robust to the exclusion of any state in Tables A10–11.

Militarized Security Interventions and Organized Crime

Our theoretical approach proposes that militarized security interventions and organized crime threats increase torture, thus working in the opposite direction of the criminal justice reform. To model the effect of militarized security interventions, this part of the analysis focuses on the Calderón presidency, when the armed forces and federal police were deployed to assist local police to combat crime through “joint operations.” Our theoretical approach stresses that arrests during these security interventions should be associated with more torture. Our model specification is as follows:

(5)$$ {\displaystyle \begin{array}{ccc}{y}_{ist}=\alpha +{\beta}_1{D}_{st}+\sum_k{\delta}_k+{\lambda}_s+{\gamma}_t+{\epsilon}_{ist},& & \end{array}} $$

where $$ {y}_{ist} $$ is a dichotomous indicator for abuse reported by prisoner $$ i $$ and $$ {D}_i $$ is an indicator variable for treatment or whether the prisoner was arrested in a state during a joint operation. The model also includes $$ k $$ individual covariates as well as unit and time fixed effects ($$ {\lambda}_s $$ and $$ {\gamma}_t $$, respectively).

Results are presented in Table 9. Model 1 shows that militarized operations substantially increase torture by almost 10 percentage points. Model 2 shows that the effect of militarized security interventions persists even after controlling for municipal-level turf wars, which also increase torture. To define turf wars, we add a dummy variable indicating that an arrest took place either in the same year as a war or where a turf war had occurred within the prior two years. As expected, turf wars are associated with more torture. Model 3 interacts joint operations with the prison jurisdiction and shows that, as expected, federal prisoners are subject to significantly more torture, but finds that joint operations worsen conditions for state and federal prisoners alike, lending support to our argument that these militarized interventions also increase torture among state-level police forces. Model 4 interacts joint operations with the arresting authority. The armed forces and federal police engage in significantly more torture than state, ministerial, and municipal police forces. There is no evidence, however, that joint operations have heterogeneous effects depending on the arresting authority.

Table 9. Effects of Militarized Security Interventions on Torture

Note: Entries are coefficients from OLS regressions, and standard errors, clustered by municipality, are in parentheses. All models include socioeconomic characteristics. We truncate the data to cover all the arrests until the end of 2012, covering the Calderón administration’s interventions but excluding arrests after that period. ***p < 0.001, **p < 0.01, *p < 0.05, ⁺p < 0.10.

In Table 10 we present placebo tests by artificially moving the date of joint operations back by one, two, and three years. We find no significant results for these “fake” joint operations. In Section 4.5 of the Online Appendix, we also explore the data for parallel trends and demonstrate that torture has similar trends in states with and without joint operations prior to the start of these security interventions. We also include models with state-specific time trends. The results are robust.

Table 10. Placebos for Federal Military Interventions

Note: Entries are coefficients from OLS regressions where we artificially move the dates of federal military interventions known as “joint operations” back by one, two, and three years. Standard errors, clustered by municipality, are reported in parentheses. Data for these tests truncate all data at the beginning of the real federal intervention to avoid including data after the real treatment is applied. All models include socioeconomic characteristics. ***p < 0.001, **p < 0.01, *p < 0.05, ⁺p < 0.10.

The Criminal Justice Reform and Organized Crime Threats

Our theoretical approach proposed that the criminal justice reform should still grant leeway to victimize suspects accused of organized crime. It also proposed that high levels of threat from organized crime should mitigate the effects of the reform. To test these hypotheses, Table 11 presents the results of various models, and analogues for brute force and threats are presented in Appendix Tables A17–A18.

Table 11. Heterogeneous Effects of the Reform: Organized Crime and Coercive Institutions

Note: Entries are coefficients from OLS regressions. Standard errors, clustered by municipality, are in parentheses. All models include socioeconomic characteristics. Analogous tables for brute force and threats are presented in Appendix Tables A17–18. ***p < 0.001, **p < 0.01, *p < 0.05, ⁺p < 0.10.

Model 1 interacts the reform with turf wars. It shows that these basically eliminate the effects of the reform, although the standard errors are large because in the post-reform era there is a small sample size of arrests during a turf war. Model 2 interacts the reform with municipal-level homicide rates. The results suggest that higher homicide rates translate into more torture. In contrast to turf wars, high homicide rates do not make the reform less effective. Model 3 interacts organized crime with the reform. As mentioned previously, the reform included a list of crimes that are excluded from some procedural protections because they are bundled into the category of “organized crime.” To operationalize this, we use the following crimes: kidnapping, drug commerce, possession of illegal weapons, and homicide. Since the law defines “organized crime” as a federal offense and those accused of this tend to be detained in federal prisons, our measure of organized crime also includes federal prisoners.Footnote ¹⁴ Model 3 shows that prisoners accused of organized crime are subject to more torture. The model also demonstrates that, as expected, the reform does not constrain abuses against criminals accused of organized crime. Model 4 shows that the reform reduces torture significantly more when the arresting authority is the ministerial police. While we note that the armed forces and federal police appear to perpetrate less torture after the reform, the standard errors are too large to reach statistical significance (likely because of the small number of observations for those arrested by these authorities after the reform).

Models in Tables 9 and 11 demonstrate that militarized interventions and the criminal justice reform have opposite effects on torture. As we examine five authorities in these models—municipal police, state police, ministerial police, the federal police, and the military—we need to correct for the increased possibility of a false discovery in these models. In the Online Appendix, we employ the approach in Benjamini and Hochberg (Reference Benjamini and Hochberg1995)Footnote ¹⁵ to control for the false discovery rate. In terms of the reform, we find that the coefficient on ministerial police remains significant. As we do not find significant heterogeneity by authority in the corresponding model in Table 9, we do not run it for joint operations. In the Online Appendix section 7, we further calculate marginal increases in torture holding the arresting authority constant. Again, we correct for the increased possibility of a false discovery and find that, consistently, torture and other forms of abuse drop significantly with the reform when the arresting authority is the ministerial police. It is at this stage in the process when coerced confessions, evidence fabrication, and witness intimidation are more likely to be carried out and where the reform has imposed more constraints. Marginal effects for the federal police and the armed forces are also negative, but they do not reach statistical significance. Finally, we find strong positive effects for the ministerial, municipal, and federal police for the case of joint operations. These results support our theory that when regular police forces act alongside the armed forces, the former engage in more torture.