Preventing criminal recruitment and careers: An Evaluation of the Parceritos program in Medellin, Colombia

The intervention, Parceritos, targets adolescent boys in Medellín identified as at moderate to high risk of criminal careers and gang recruitment. The program consists of two main components: (i) an informational/experiential component and (ii) a behavioral skill-building component.

The informational/experiential component is designed to address a set of common misperceptions that are associated with crime and gang interest: an underestimation of the range of legal opportunities available (and the returns to education), a misunderstanding of the tertiary educational opportunities and costs, and a lack of identification with these careers. Participants visit tertiary vocational schools, universities, and employers to understand the accessibility of higher education and skilled careers, learn about free education options, and meet people from their neighborhoods in these schools and careers.

The behavioral change intervention is called WOOP (Wish, Outcome, Obstacle, Plan). It is a structured process that fosters goal-setting, motivation, planning, and mental contrasting as an innate, automatic skill. In addition to helping students learn to set concrete, meaningful goals, it emphasizes two additional cognitive processes thought to be important to staying motivated and attaining one’s goals: vividly imagining potential obstacles (mental contrasting) and forming concrete plans to overcome those obstacles through “if-then” thinking (“implementation Intentions”). Participants practice setting goals and planning around obstacles on a small day-to-day scale and over longer timeframes.

The intervention is implemented across 8 sessions, each one up to 8 hours long, out of school, in groups of about 25, over the course of several weeks.

The program is principally targeted at boys in grades 6-9, with an emphasis on grades 7 and 8. To screen and recruit moderate to high-risk adolescent boys, we screen and stratify boys both by self-reported risk and interest in criminal careers, as well as through a predicted risk algorithm.

We identified an initial experimental sample (Cohort 1) of 1,476 boys from a pool of 10,000. 365 of these subjects were assigned to receive Parceritos between October 2024 and April 2025. We anticipate a Cohort 2 of roughly similar size to be selected from a March-May 2025 screening of an additional 10,000 boys to receive the program in August-November 2025 (estimated).

2024-08-15

2025-06-15

For the first short term endpoint—12 months following the end of the intervention—the primary outcome is continued school enrollment (i.e. dropout). Our proxy for this is a failure to appear in the national school register, supplemented where possible with additional data from the school, family, or student to account for any potential errors in the national registry. We will be able to monitor impacts on school enrollment at regular intervals following the first endpoint.

Longer term, our preferred primary outcome is an aggregate index of school attainment and criminal and gang engagement. If the data become available, we envisage a standardized index that averages measures of: (i) school attainment/dropout; (ii) general criminal engagement; and (iii) gang involvement. We are interested in the overall impact on this index as well as on the individual components (adjusted for the number of relevant comparisons).

As discussed below, there is some uncertainty as to what data and outcomes will be available, and so the number and nature of the components will adapt to the available data.

Based on correlational and structural analysis of baseline data on 10,000 youths, our hypothesis is that some adolescent boys leave school and enter criminal careers in part because they underestimate the quality and availability for their non-criminal options. Thus we hypothesize that Parceritos will lead higher-risk adolescents to be more likely to choose to complete secondary school, enter tertiary education, and seek non-criminal careers. Membership in a drug-selling gang is one of the most common criminal careers in Medellin, but involvement in theft and other crime is also common.

Of course we can only proxy for these choices, and there are many options available. Our approach is guided by the wish to use the most accurate measures available, while minimizing the number of hypotheses tested. Our choice of a primary index with educational and criminal components is guided by this.

While the subjects are minors, the main measure of school attainment is continued secondary school enrolment. Other schooling outcomes (such as school performance) will be secondary or exploratory outcomes, as described below.

Measuring criminal engagement is more challenging, especially with minors. Juvenile detention and arrest records exist, both within the criminal justice and school and social protection systems. In addition to formal arrest records, there also appear to be records of minors who are involved with the city’s various juvenile corrections and reporting systems. Access to these systems is feasible and legal, but requires obvious procedural and legal and privacy steps to take place before we can evaluate the exact nature and quality of the data and use it to evaluate impacts. Therefore, it is possible that we may not have administrative data on criminal justice involvement until the subjects are adults and enough time has passed for some to become engaged in the criminal justice system. At that time, we anticipate that adult criminal arrest or detention will be the main administrative measure of criminal engagement.

Of course, arrest is a poor proxy for criminal engagement and a noisy indicator of gang membership. Hence, after the intervention is completed we will pilot and develop a more direct measure. The most likely proxy for gang membership will be a one we construct using a combination of direct surveys of the sample, surveys, and interviews with their close associates and community, police records, and direct observation. We will update our pre-registration to report this outcome before collecting and analyzing the data.

This is a longitudinal study and we expect to measure secondary and exploratory outcomes over the lifecycle. We will generally not adjust analysis for multiple comparisons for these more exploratory outcomes.

First-stage outcomes. In addition to participation in the program on the intensive and extensive margins, we may survey the experimental sample on their beliefs about the cost of and the returns to schooling, as well as the relative returns to criminal and non-criminal careers (akin to the baseline measures).

Other schooling outcomes. In addition to enrollment, we will seek data on school performance, disciplinary records, etc. With the exception of grade 11 standardized test scores, at present schools do not systematically collect such data in a consistent and centralized fashion, but we are helping them develop these capabilities and more measures may become available depending on the systems developed by the school system.

Long-term outcomes: Longer term we will be able to observe in administrative data tertiary educational choices, occupational choices, lifetime earnings in the formal sector, and participation in social welfare programs.

For Cohort 1, our core experimental sample consists of 1,476 moderate- to high-risk boys who completed our survey in 52 schools. There was a 2-stage randomization. Half (26) of the schools were randomly assigned to have their pupils be eligible for treatment. Within schools eligible for treatment, half of the moderate- to high-risk boys enrolled at the time of randomization were assigned to treatment. This results in three experimental conditions: treatment boys, spillover boys (control boys in treatment schools), and pure control boys (control boys in control schools).

We expect Cohort 2 to follow a similar design for a pooled experimental sample of approximately 3,000 pupils in 100 schools.

Finally, prior to Cohorts 1 and 2, we conducted a pilot program and evaluation with an experimental sample of 250 youth in 6 schools. Four schools were assigned to treatment and students were assigned to the program within schools at random, stratified by baseline risk level. We had access to 9-month post-intervention results of the pilot before registering the full experimental design. We did not have access to any post-randomization data on Cohort 1 prior to registration (Cohort 1 is currently undergoing the intervention at the time of registration).

ESTIMATION OF DIRECT TREATMENT EFFECTS

We are primarily interested in direct treatment effects. Spillover effects are of secondary interest, and more exploratory, given that we do not have strong priors about the direction or magnitude of spillovers. We will return to this below.

For average treatment effects, we will estimate the simple intent-to-treat (ITT) effect of treatment as well as the effect of treatment on the treated (TOT). TOT uses individual random assignment as an instrument for a “treated” indicator. We define “treated” as equaling one if the pupil attended at least one session of the program and zero if they declined to participate or never attended (e.g. because they transferred to another school before the program began).

We plan to run the following OLS regression:

y = 𝛿T + 𝜃S + 𝛽X + 𝜀

where:
y is the outcome
T = 1 for students assigned to treatment and is 0 for spillover and pure controls
S is a vector of spillover variables, discussed below
X is a vector of baseline covariates (school and pupil level) selected via a double lasso method, plus fixed effects for the cohort

For the ITT we are interested in 𝛿. As mentioned, we will also estimate the TOT estimate, using T as an instrument for treated.

HETEROGENEITY ANALYSIS

Our main heterogeneity analysis will look at impacts by baseline criminal recruitment risk level. We will use baseline self-reported risk and a set of risk factors (all other baseline survey and baseline school variables) to train a predictive model to develop a measure of predicted recruitment risk. We will estimate treatment heterogeneity by interacting treatment status with an indicator of “moderate” recruitment risk (as opposed to “high” risk). We expect this to be an indicator of being below-median predicted risk within the experimental sample. We will also explore alternative subgroups/specifications as supplemental analyses.

ESTIMATION OF SPILLOVERS

Spillovers are a secondary analysis partly because we probably do not have the statistical power to detect all but relatively large spillovers (see power analysis below). What’s more, there may be countervailing effects that reduce estimated spillovers on net. On the one hand, positive informational and behavioral spillovers could improve school dropout, criminal engagement, and gang entry. On the other hand, if demand for labor in the gangs is relatively inelastic, then this could result in negative spillovers to criminal careers and gang membership.

There are several options for improving statistical power and disentangling these countervailing effects. One is to take advantage of the fact that we have partial social network data for surveyed students (up to 10 friends in the school, a subset of whom would have answered our survey and also be eligible for the experimental sample based on risk). The other is to take advantage of the fact that we will have administrative data (such as school dropout, and eventually arrest data) on all classmates, including the lower risk students and the students who did not answer the survey. Finally, there will be random variation in the degree to which the number of friends are treated.

Thus we expect the vector S to include:
An indicator for the spillover condition
A measure of friends treated
The total number of friends in the experimental sample and the total number of friends they listed in their cohort

Note that the coefficients on #3 are not of substantive interest. As for #2, the number of friends and the proportion of friends treated should yield substantively the same coefficient. We can also use an indicator for any friends treated. Since, for cohort 1, the majority of the experimental sample have only 1 friend treated, this indicator should yield qualitatively similar results to the proportion, and if so, is more easily interpreted. But the default would be to use the proportion for accuracy, especially if the results are not qualitatively the same.

We will consider alternate specifications. Note that our primary estimate of interest, the direct treatment effect 𝛿, should not be significantly affected by the specific vector of spillover variables used.

We will calculate spillover effects first within the “core” experimental sample, but also within the broader sample. The core sample of 1,476 excludes pupils in the same classrooms who were designated “low risk”, or who did not complete the risk assessment survey. A broader experimental sample would include them, along with indicators for each of these strata.

Not available

We conducted the randomization using Stata. Procedures below.

Cohort 1: In a first stage (school-level randomization) we stratified the 52 schools into 13 strata of 4 schools each, based on the school’s total number of moderate- and high risk pupils. Two schools in each strata were randomly assigned to have their pupils eligible for treatment, leading to 26 treatment schools and 26 control schools. In the second stage (pupil-level randomization within schools eligible for treatment) half of the moderate to high risk students were assigned to treatment using a random variable. Prior to this procedure, we dropped from the eligible experimental sample any pupils that were not listed as officially registered as of the month prior to randomization (i.e. students who transferred schools or left school between the time of survey and the randomization). We set an algorithm that conducted this 2-stage randomization 4000 times and selected the randomization with the highest level of balance in two multivariate regressions: of treatment (T) on a selection of 5 school-level and 18 pupil-level covariates and spillovers (S) on the same covariates. This resulted in a core experimental sample of 1476 moderate to high risk boys, 365 being assigned to treatment, 353 to spillover status, and 758 to pure control stats (in control schools).

No

Cohort 1: Treatment is randomized at the pupil level within 52 schools.

Cohort 1: The core experimental sample is 1476 moderate- to high-risk male pupils in 52 schools.

Cohort 1: Of the 52 schools, 26 were assigned to have students eligible for treatment, and 26 were assigned to control status. Within treatment schools, we assigned students to treatment with a 50% probability.

For cohorts 1 and 2 pooled, we anticipate a treatment group of approximately 600 boys in 100 schools. For power analysis, we conduct an 80% power, 2-sided test with a significance level of 0.05. From our Cohort 1 baseline survey data, we estimate an intracluster correlation of 0.02 among the subset of high-risk youths in the sample and assume an R-squared of 0.15. Under these conditions, we calculate a minimum detectable effect (MDE) of 0.13 standard deviations (0.11 for a significance level of 0.1). Should Cohort 2 fail to happen, we calculate an MDE of 0.18 standard deviations. Note that, while we are powered to detect direct treatment effects, spillover effects into general peers or friends are likely to be considerably smaller. Even an experiment an order of magnitude larger may not identify spillover effects under 0.1 standard deviations. This is why the highest likelihood of finding spillovers will happen within the close social network.