• We are sorry, but NCBI web applications do not support your browser and may not function properly. More information
Logo of amjepidLink to Publisher's site
Am J Epidemiol. May 15, 2012; 175(10): 1045–1053.
Published online Apr 2, 2012. doi:  10.1093/aje/kwr428
PMCID: PMC3353133

Reducing Violence by Transforming Neighborhoods: A Natural Experiment in Medellín, Colombia


Neighborhood-level interventions provide an opportunity to better understand the impact that neighborhoods have on health. In 2004, municipal authorities in Medellín, Colombia, built a public transit system to connect isolated low-income neighborhoods to the city’s urban center. Transit-oriented development was accompanied by municipal investment in neighborhood infrastructure. In this study, the authors examined the effects of this exogenous change in the built environment on violence. Neighborhood conditions and violence were assessed in intervention neighborhoods (n = 25) and comparable control neighborhoods (n = 23) before (2003) and after (2008) completion of the transit project, using a longitudinal sample of 466 residents and homicide records from the Office of the Public Prosecutor. Baseline differences between these groups were of the same magnitude as random assignment of neighborhoods would have generated, and differences that remained after propensity score matching closely resembled imbalances produced by paired randomization. Permutation tests were used to estimate differential change in the outcomes of interest in intervention neighborhoods versus control neighborhoods. The decline in the homicide rate was 66% greater in intervention neighborhoods than in control neighborhoods (rate ratio = 0.33, 95% confidence interval: 0.18, 0.61), and resident reports of violence decreased 75% more in intervention neighborhoods (odds ratio = 0.25, 95% confidence interval 0.11, 0.67). These results show that interventions in neighborhood physical infrastructure can reduce violence.

Keywords: causality, economic development, environment, neighborhood, residence characteristics, violence

Violence is a major cause of death and disability worldwide (1). According to the World Health Organization, 1,424 people die in acts of homicide on an average day—1 homicide per minute, on average—and many more are victims of nonfatal violence (1). Thus, violence contributes significantly to the global burden of injury and disability and the cost of health and welfare services (1, 2).

There is a long line of research linking the prevalence of violence to neighborhood factors such as concentrated disadvantage, residential instability, and the absence of “collective efficacy” (310). Moreover, many antiviolence initiatives target neighborhoods rather than individuals—for example, efforts to improve public spaces and infrastructure, have police engage more with the community, clean up debris, and reduce social disorder—in the hopes that changing environments will trigger widespread and long-lasting reductions in violence (1116).

Still, many critics dismiss the evidence for “neighborhood effects” as resting on observational studies in which neighborhood treatment conditions are not randomly assigned and are probably confounded by unobserved factors that determine both the outcome (e.g., violence) and where a person lives (17, 18). One of the few attempts to study the effects of randomly assigned neighborhood conditions was the Moving to Opportunity experiment, conducted among publicly housed families from poor urban neighborhoods in 5 US cities (19), where the treatment was an opportunity to move away from poor neighborhoods via a housing voucher (2022). The results have been mixed. Although male and female youth from families that received vouchers to relocate to lower-poverty areas experienced declining involvement in violent crimes, male youth also experienced more conduct disorder, other problem behaviors, and property crime arrests (23). A key limitation of Moving to Opportunity and other studies of voucher programs is that the neighborhood effects they identify are moves to new neighborhoods rather than changes in current neighborhoods. Moreover, such studies cannot disentangle the potentially disruptive effects of a residential move from the potentially beneficial effects of living in a less impoverished neighborhood.

One way to address the limitations of observational studies and voucher-based experimental studies of neighborhood effects is to conduct randomized interventions that change neighborhoods rather than move individuals to new neighborhoods. Such a project would require a staggering commitment of resources and political capital in order to 1) implement a sufficiently effective intervention, 2) deny the intervention to a randomly selected control group of neighborhoods, and 3) collect data on large samples of neighborhoods and individuals, before and after the intervention. Although community trials are common in epidemiologic research, such studies tend to be based on a small number of neighborhoods, and often the intervention is not randomly assigned (2426).

In cases where large-scale social experiments are prohibited for practical or ethical reasons, researchers often look for “natural experiments”—usually changes resulting from policies, interventions, or acts of nature—that exogenously assign treatment conditions, but we are aware of few prior attempts to test neighborhood-effect hypotheses using a natural experiment (27). The current study fills this void by capitalizing on a large-scale natural experiment resulting from a public works project in a subset of neighborhoods from a major Latin American city: Medellín, Colombia.

Using data contemporaneously collected on Medellín neighborhoods that were targeted by the public works project and a matched set that were not, we assessed whether neighborhoods that received the intervention experienced significantly greater 1) declines in violence and 2) corresponding improvements in neighborhood conditions that might contribute to reductions in violence, including collective efficacy, citizens’ trust in the criminal justice system and reliance on police, and the availability of neighborhood amenities such as parks and cultural activities.


The intervention

Medellín is Colombia’s second-largest city, with a population of over 3 million in the metropolitan area (28). Fueled by drug-related conflict involving the Medellín drug cartel and various paramilitary gangs, it became one of the most violent cities in the world during the 1980s and 1990s. Homicide has been the leading cause of death in Medellín since 1986 (29). In 2002, before the intervention, Medellín’s homicide rate was 185 per 100,000 population, accounting for 28% of deaths in the city (30). By comparison, the highest homicide rate in a US city in 2002 was 53 per 100,000 population, in New Orleans, Louisiana (31).

In 1999, the municipal government of Medellín enacted a territorial plan to promote urban and rural development, which included a cable-propelled transit system (gondola) known as Metrocable (32). The first line (K) opened in 2004, connecting an elevated train system in the city center to the impoverished Santo Domingo neighborhood in the mountainous periphery, with 4 stops covering a distance of 2,072 m and reaching an elevation of 399 m (33). The municipal government made other improvements to neighborhoods serviced by the gondola, including additional lighting for public spaces; new pedestrian bridges and street paths; “library parks”; buildings for schools, recreational centers, and centers to promote microenterprises; more police patrols; and a family police station next to a gondola station. The locations were selected by a panel of municipal authorities on the basis of topographic and geographic feasibility.

Study design

Most of our preintervention data came from a 2003 household survey on neighborhoods and violence known as Prevención de Violencia en el Valle de Aburrá (PREVIVA), or Violence Prevention in the Valley of Aburrá, conducted in a representative sample (n = 2,500) of Medellín’s noninstitutionalized population aged 12–60 years. A sample of 212 blocks was selected from each of the city’s 16 districts, with probability proportionate to the size of the district’s population aged 12–60 years, and 12 residents were selected per block, with probability inversely proportionate to size, so that the sample would be self-weighting (34). The response rate was 90.3%. In 2008, we conducted follow-up interviews with 466 of the 599 PREVIVA respondents (78%) who at baseline had resided in 1) one of the 25 study neighborhoods where the first gondola system was installed (City Districts 1 and 2) or 2) one of 23 study neighborhoods located in comparable city districts (4 and 8) that were not serviced by the gondola system. We refer to the first set of neighborhoods as the “intervention group” and the second as the “control group.”

To choose neighborhoods for the control group, we performed an agglomerative cluster analysis (35) of all 16 city districts and selected PREVIVA neighborhoods that clustered with City Districts 1 and 2. The variables used in this analysis included indicators of service infrastructure (number of schools, sports sites, health centers), a classification of “socioeconomic stratification” based on official evaluations of city blocks used for property tax assessments, the proportion of residents eligible for welfare (from the Municipal Office of Planning), and average levels of antisocial behavior and collective efficacy (from the baseline PREVIVA survey). Web Figure 1 (available on the Journal’s website (http://aje.oxfordjournals.org/)) shows the locations of intervention and control neighborhoods.

The resulting sample contained 225 respondents from intervention neighborhoods and 241 respondents from control neighborhoods. Intervention- versus control-group status was based on where respondents resided during the baseline interview, so our estimates represent the “intent-to-treat” effect and may underestimate the treatment’s effects on persons who were fully exposed to it. At the time of the follow-up interview, most respondents (n = 484; 81%) were still living in their baseline neighborhood, and of the 115 respondents who left, only 45 (7.5%) moved from an intervention-group neighborhood to a control-group neighborhood or vice versa.


We constructed neighborhood-level outcome measures of violence and the local social/institutional climate (Table 1) from the multilevel measurement models described below. The violence measures included 1) survey reports of violent events occurring in the neighborhood during the past 6 months and 2) annual neighborhood-level homicide event counts in 2003–2008 from the Office of the Public Prosecutor. The other outcome measures included survey-based scales of 1) collective efficacy (modified version of the scale developed by Sampson et al. (6), including questions about the likelihood of neighbors taking action in situations that threaten the social order and about their willingness to help one another), 2) trust in the criminal justice system (including the police, the family welfare system, judges, and prosecutors), 3) reliance on police to help solve neighborhood problems, and 4) the presence of neighborhood amenities (including parks, recreational centers, and cultural activities).

Table 1.
Characteristics (%a) of Intervention and Control Neighborhoods Before and After the 2004 Introduction of a Public Transit System and Infrastructure Improvements, Medellín, Colombia, 2003–2008


We first tested the preintervention balance between the intervention and control groups with regard to covariates and baseline measures of outcomes, to determine whether differences were large enough to warrant further adjustment via matching. We employed an omnibus balance test that compares the Mahalanobis distance between groups on characteristics (Table 2) with a probability distribution generated by randomly assigning intervention and control labels to neighborhoods across all permutations (36). This approach avoids the problems of performing multiple tests and is robust in small samples (n = 48 neighborhoods) (37). Finding matching to be warranted, we used a Bayesian logistic regression model to estimate each neighborhood’s propensity of receiving the intervention, conditional on covariates listed in Table 2 (38), and matched neighborhoods on their propensity scores using the optmatch tool in R (37). We summarized the matched, preintervention differences using a similar omnibus balance statistic, assessing it against the matched permutation distribution of such statistics, the distribution induced by independently randomizing intervention and control labels within each matched set.

Table 2.
Baseline Characteristics of Intervention and Control Neighborhoods Before Propensity Score Matching, Medellín, Colombia, 2003

To measure change over time, we fitted hierarchical generalized linear models (HGLMs) for each outcome on pooled pre- and postintervention data. For the survey-based outcomes, we used a logit link function to regress responses to the binary items in a given scale on 1) item dummy variables, 2) a postintervention versus preintervention dummy variable, and 3) individual- and neighborhood-level random effects for the intercept and postintervention dummy variable. We fitted another HGLM to neighborhood homicide rates, using a Poisson distribution, a log link function, and random effects for neighborhoods only (see Web Appendix for details). Interpreting the neighborhood-level random component of the post- versus preintervention terms as change scores, we tested for the presence of treatment effects by comparing mean differences of intervention and control neighborhoods’ change scores with the distribution of means of such differences obtained by permuting intervention and control labels within matched sets. This layering of permutation tests over parametric measurement models excludes the possibility of findings that are falsely significant because of “interference” across neighborhoods or misspecification of the measurement model (3941).

To produce confidence intervals and point estimates, we iteratively tested a series of null hypotheses, each positing a uniform treatment effect of a given size t. Hypotheses with t = 0 correspond to the tests for the presence of a treatment effect just described; to test each hypothesis positing a nonzero t, we estimated an HGLM with an offset term for the intervention group of size t, so that if the group differences in change were equal to t, the change scores for the two groups would be approximately equal. The Hodges-Lehmann estimate (42) of the treatment effect is then the value of t giving rise to an estimated HGLM in which matched differences between intervention and control neighborhoods’ change scores most nearly average to zero. For hypothesis tests, neighborhood change scores were extracted from each model and the mean of their matched differences was compared with its permutation distribution, yielding a 2-sided test with a significance level of α = 0.05.

If the null hypothesis was sustained, the hypothesized treatment effect was included in the confidence interval (i.e., t was considered one of the plausible values of the actual treatment effect). We iterated this estimation and testing procedure using progressively larger values of t to determine the upper limit of the 95% confidence interval, and we also tested negative values of t when necessary to determine the confidence interval’s lower limit.

We subjected all significant findings to sensitivity analysis to determine how high the correlation between an unobserved confounder and the intervention variable would have to be to reduce the treatment effect to nonsignificance (42). Confounding with the intervention variable was summarized using Rosenbaum’s gamma, which indicates the proportionate amount by which a neighborhood’s odds of receiving the intervention could be increased/decreased by the unobserved confounder (see Web Appendix for details).


Table 1 presents group-level means for each time period and the corresponding percentage changes for the outcome scales and their component items. Because these results serve descriptive purposes, no hypothesis tests are presented in Table 1. Levels of homicide and perceived violence declined in both groups, but the drop was steeper in the intervention group, where the homicide rate dropped by 84% as compared with 60% in the control group, and the proportion of respondents endorsing the average item (i.e., responding “yes” to a prototypical item) in the violence scale dropped by 90% as compared with 74% in the control group. Collective efficacy increased in the intervention group but remained stable in the control group. For example, the proportion of intervention-group respondents reporting that their neighbors would intervene to break up a fight among children increased from 65% to 81%, while the corresponding proportion in the control group was 71%–72% at both time points. Trust in the criminal justice system and reliance on the police for help also increased more dramatically in the intervention group. For example, the proportion of respondents who said they would call the police if they saw suspicious activity increased by 77% over time in the intervention group as compared with a 14% increase in the control group. The reported prevalence of parks and recreational areas did not change over time in either group, but reports of local opportunities to participate in cultural and educational activities increased in the intervention group.

Selection of neighborhoods for the intervention appears to have been driven by geographic and topographic factors, which might potentially have been correlated with relevant baseline variables. Table 2 compares intervention and control groups with regard to 23 such variables, mostly finding differences no larger than would be expected if all neighborhoods had precisely the same propensity to be selected for the intervention. Combining these baseline differences into an omnibus test, the hypothesis of simple randomization of neighborhoods was narrowly sustained (χ2 = 30.5 (21 degrees of freedom (df)); P = 0.08). Still, we propensity-score-matched intervention and control neighborhoods to ensure that the degree of balance in our analytic sample would be at or above the second quartile of the reference distribution produced by simple random assignment. This yielded 21 matched pairs and 2 triplets, pairs of higher-propensity treatment neighborhoods matched to a shared control. A subsequent balance test placed the combined baseline difference between matched intervention and control neighborhoods within the second quartile of a reference distribution corresponding to matched random assignment (χ2 = 21.3 (21 df); P = 0.44). The outcome analyses that followed would assume this paired assignment model.

Figure 1 shows the estimated change in each outcome for the matched intervention and control groups along with estimated group differences in change (“difference-in-difference” estimates) and confidence intervals. The group differences for change in both homicide and perceived violence were significant at the 5% level under 2-sided tests. Compared with the control group, the intervention group experienced a 66% (0.66 = 1 − exp[−1.1]) greater drop in the homicide rate (95% confidence interval (CI): −1.7, −0.5) and a 75% (0.75 = 1 − exp[−1.4]) greater drop in the odds of reported violence (95% CI: −2.2, −0.4). Sensitivity analysis revealed that these effects were robust, as an unobserved variable would need to increase the odds of treatment by at least 80% (γ = 1.8) in the case of homicide and by 20% (γ = 1.2) for perceived violence in order to confound the estimated treatment effects.

Figure 1.
Diminishing violence in 25 Metrocable intervention (I) neighborhoods and 23 matched control (C) neighborhoods, Medellín, Colombia, 2003–2008. Violence decreased in both groups of neighborhoods, but intervention-group neighborhoods enjoyed ...

None of the other difference estimates were significant at the 5% level in 2-sided tests (Figure 2). However, reliance on the police increased 2.5 times more (exp[0.9]; 95% CI: −0.2, 1.8) in the intervention group; this difference would have been significant in a 1-sided test reflecting our a priori hypotheses (P = 0.043), and it is significant at the 10% level (P = 0.086) in a 2-sided test. In addition, collective efficacy grew 1.5 times more (exp[0.4]; 95% CI: −0.2, 1.1) in the intervention group than in the control group, a difference that would be marginally significant (P < 0.075) in an appropriate 1-sided test.

Figure 2.
Improvement in community resources in 25 Metrocable intervention (I) neighborhoods (black bars) and 23 matched control (C) neighborhoods (gray bars), Medellín, Colombia, 2003–2008. Conditions improved in both groups of neighborhoods, but ...


Despite the increasing popularity of place-based interventions and the considerable body of evidence from observational studies linking neighborhood conditions to the prevalence of violence and other health outcomes, skepticism remains about the credibility of the findings and the wisdom of using them to inform interventions (18, 4345). Many critics and proponents of these studies agree that in the absence of a neighborhood randomized controlled trial, researchers should seek out natural experiments in which the assignment of a treatment condition closely approximates randomization. A large place-based intervention provides conditions for a natural experiment as well as the opportunity to assess the benefits to public health of policies that target neighborhood environments, even if those policies are not explicitly designed to improve health.

The fortunate coincidence in Medellín of a preintervention household survey (PREVIVA) and a large-scale public works project (Metrocable), wherein treatment was plausibly assigned to neighborhoods on the basis of exogenous factors, provided an unprecedented opportunity to study a natural experiment on neighborhood effects. We took several steps to ensure that we had the strongest case for causal inference. First, we took advantage of a naturally occurring exogenous source of neighborhood change to address the concern of self-selection of individuals into neighborhoods. Second, we used cluster analysis to select comparable control neighborhoods and then matched neighborhoods on their propensity scores to ensure that the groups were as comparable as would be expected under randomization. Third, we used randomization-based inference to conduct hypothesis tests that remained valid even in the presence of potential threats to causal inference, such as treatment “spillover.”

The intervention was associated with significant declines in neighborhood violence: The drop in homicide between 2003 and 2008 was 66% times higher in intervention neighborhoods than in control neighborhoods, while the corresponding drop in reports of violent events was 74% higher in intervention neighborhoods. Residents of intervention neighborhoods also experienced more growth in willingness to rely on the police and perceptions of collective efficacy, although these effects were marginally significant (the latter only in a 1-sided test). We found little evidence of an intervention effect on the presence of neighborhood amenities, but our ability to detect treatment effects on amenities was constrained by the broad nature of preintervention survey questions (which were replicated in follow-up interviews) that asked only about the presence of amenities and not about aspects of their condition that may have been improved by the intervention.

Although our study was not designed to investigate the mechanisms that produced the observed drops in violence, one account that is consistent with the pattern of changes we observed is that by improving public spaces and creating new institutions, the intervention provided more opportunities for neighbors to interact, develop trust, and become willing to intervene when the social order was threatened (5, 6). It also appears that relations between citizens and police improved in intervention neighborhoods, which could increase the efficacy of law enforcement in fighting violence and further deter would-be violent offenders (46).

Our study illustrates how the benefits of place-based interventions can diffuse beyond their intended areas of impact. The government’s principal motivation for bringing effective public transportation to remote areas of Medellín was to improve residents’ access to jobs and attract new businesses to impoverished neighborhoods. Reducing levels of violence, generating more collective efficacy, and increasing reliance on police appear to be downstream benefits of the dynamics set in place by the investment in public works. Another recent study provides a similar example by showing how the installation of a light rail transit system in North Carolina was associated with declining obesity and increasing physical activity in the affected areas (27).

There were several limitations of the study. First, we could not rule out the possibility that unobserved factors confounded our estimated treatment effects. This concern is allayed, however, by the exogenous nature of the intervention, the extensive set of covariates used in propensity score matching, and a series of sensitivity analyses assessing the effect of the intervention under assumptions of comparison group mismatch. Second, our design was not equipped to explain the mechanisms responsible for the decline in violence. Such an investigation would require additional sources of exogenous variation and a factorial design to assess how different combinations of treatment assignment and factors representing potential treatment mechanisms affected violence. However, the documented change in neighborhood conditions that accompanied the gondola intervention provides preliminary evidence on the mechanisms that explained the change in risk behaviors over time. Third, it is difficult to generalize from the results of this wide-ranging public works intervention to draw lessons for specific types of interventions. Our intent in this study was to examine whether large-scale investments in neighborhood infrastructure can be linked to measurable changes in violent activity, not to identify what types of investments are likely to have the most payoff.

The evaluation of Metrocable represents one of the first natural experiments on neighborhoods and violence, and the first, to our knowledge, in a developing country. Our findings have potential policy implications for urban settings beyond Medellín and indicate that it is possible, even in low- to middle-income countries, to harness municipal resources to implement structural interventions that will have an important impact on risk behaviors that place a significant burden on the health of populations.

Supplementary Material

Web Material:


Author affiliations: Department of Epidemiology, Mailman School of Public Health, Columbia University, New York, New York (Magdalena Cerdá); Department of Sociology, College of Literature, Science, and the Arts, University of Michigan, Ann Arbor, Michigan (Jeffrey D. Morenoff); Department of Statistics, College of Literature, Science, and the Arts, University of Michigan, Ann Arbor, Michigan (Ben B. Hansen, Kimberly J. Tessari Hicks); Escuela Nacional de Salud Pública, Universidad de Antioquia, Medellín, Colombia (Luis F. Duque, Alexandra Restrepo); and Department of Epidemiology, School of Public Health, University of Michigan, Ann Arbor, Michigan (Ana V. Diez-Roux).

This work was supported by the Robert Wood Johnson Foundation Health and Society Scholars Small Grants Program (grant to M. C.), the University of Michigan Population Studies Center Weinberg and Freedman Funds (a Weinberg Fund grant to M. C. and a Freedman Fund grant to J. M.), and the National Institute on Drug Abuse (grant K01DA030449-01 to M. C.).

The authors thank Nilton Montoya of the Universidad de Antioquia for his assistance in the design of the study.

Conflict of interest: none declared.



confidence interval
hierarchical generalized linear model
Prevención de Violencia en el Valle de Aburrá


1. Krug E. World Report on Violence and Health. Geneva, Switzerland: World Health Organization; 2002.
2. Reza A, Mercy JA, Krug E. Epidemiology of violent deaths in the world. Inj Prev. 2001;7(2):104–111. [PMC free article] [PubMed]
3. Krivo LJ, Peterson RD. Extremely disadvantaged neighborhoods and urban crime. Soc Forces. 1996;75(2):619–648.
4. Pratt TC, Cullen FT. Assessing macro-level predictors and theories of crime: a meta-analysis. Crime Justice Rev Res. 2005;32:373–450.
5. Morenoff JD, Sampson RJ, Raudenbush SW. Neighborhood inequality, collective efficacy, and the spatial dynamics of urban violence. Criminology. 2001;39(3):517–559.
6. Sampson RJ, Raudenbush SW, Earls F. Neighborhoods and violent crime: a multilevel study of collective efficacy. Science. 1997;277(5328):918–924. [PubMed]
7. Sampson RJ, Groves WB. Community structure and crime—testing social-disorganization theory. Am J Sociol. 1989;94(4):774–802.
8. Jacob JC. Male and female youth crime in Canadian communities: assessing the applicability of social disorganization theory. Can J Criminol Crim Justice. 2006;48(1):31–60.
9. Van Wilsem J, Wittebrood K, De Graaf ND. Socioeconomic dynamics of neighborhoods and the risk of crime victimization: a multilevel study of improving, declining, and stable areas in the Netherlands. Soc Probl. 2006;53(2):226–247.
10. Villarreal A, Silva BFA. Social cohesion, criminal victimization and perceived risk of crime in Brazilian neighborhoods. Soc Forces. 2006;84(3):1725–1753.
11. Leventhal T, Brooks-Gunn J. The neighborhoods they live in: the effects of neighborhood residence on child and adolescent outcomes. Psychol Bull. 2000;126(2):309–337. [PubMed]
12. Cytron N. Improving the Outcomes of Place-based Initiatives. San Francisco, CA: Federal Reserve Bank of San Francisco; 2010.
13. Mercado S, Havermann K, Nakamura K, et al. Responding to the Health Vulnerabilities of the Urban Poor in the “New Urban Settings” of Asia. New York, NY: Center for Sustainable Urban Development, Earth Institute, Columbia University; 2007.
14. Commission to Build a Healthier America, Robert Wood Johnson Foundation. Beyond Health Care: New Directions to a Healthier America. Princeton, NJ: Robert Wood Johnson Foundation; 2010.
15. Braga AA, Bond B. Policing crime and disorder hot spots: a randomized controlled trial. Criminology. 2008;46(3):577–607.
16. Hope T. Community crime prevention. In: Tonry M, Farrington D, editors. Building a Safer Society. Chicago, IL: University of Chicago Press; 1995. pp. 21–89.
17. Mayer SE, Jencks C. Growing up in poor neighborhoods: how much does it matter? Science. 1989;243(4897):1441–1445. [PubMed]
18. Oakes JM. Commentary: advancing neighbourhood-effects research—selection, inferential support, and structural confounding. Int J Epidemiol. 2006;35(3):643–647. [PubMed]
19. Kling JR, Liebman JB, Katz LF. Experimental analysis of neighborhood effects. Econometrica. 2007;75(1):83–119.
20. Clark WA. Intervening in the residential mobility process: neighborhood outcomes for low-income populations. Proc Natl Acad Sci U S A. 2005;102(43):15307–15312. [PMC free article] [PubMed]
21. Rosenbaum JE, Zuberi A. Comparing residential mobility programs: design elements, neighborhood placements, and outcomes in MTO and Gautreaux. Hous Policy Debate. 2010;20(1):27–41.
22. Stal GY, Zuberi DM. Ending the cycle of poverty through socio-economic integration: a comparison of Moving to Opportunity (MTO) in the United States and the Bijlmermeer Revival Project in the Netherlands. Cities. 2010;27(1):3–12.
23. Kling JR, Ludwig J, Katz LF. Neighborhood effects on crime for female and male youth: evidence from a randomized housing voucher experiment. Q J Econ. 2005;120(1):87–130.
24. Morenoff J, Diez Roux A, Hansen B, et al. What can we learn about policy interventions from observational studies? In: Schoeni R, House J, Kaplan G, et al., editors. Making Americans Healthier: Social and Economic Policy as Health Policy. New York, NY: Russell Sage Foundation; 2008. pp. 309–343.
25. Wagenaar AC, Murray DM, Gehan JP, et al. Communities mobilizing for change on alcohol: outcomes from a randomized community trial. J Stud Alcohol. 2000;61(1):85–94. [PubMed]
26. Forster JL, Murray DM, Wolfson M, et al. The effects of community policies to reduce youth access to tobacco. Am J Public Health. 1998;88(8):1193–1198. [PMC free article] [PubMed]
27. MacDonald JM, Stokes RJ, Cohen DA, et al. The effect of light rail transit on body mass index and physical activity. Am J Prev Med. 2010;39(2):105–112. [PMC free article] [PubMed]
28. Administrative Department of Population, Mayor’s Office of Medellín. Medellín y su Población. Medellín, Colombia: Alcaldía de Medellín; 2005. ( www.medellin.gov.co/alcaldia/jsp/modulos/P_ciudad/pot/Acuerdo%2046/4%20MEDELLIN%20Y%20SU%20POBLACION.pdf). (Accessed May 8, 2011)
29. Cardona M, García HI, Giraldo CA, et al. Homicides in Medellín, Colombia, from 1990 to 2002: victims, motives and circumstances [in Spanish] Cad Saude Publica. 2005;21(3):840–851. [PubMed]
30. Observatorio de la Violencia. Medellín: Compromiso de Toda la Ciudadanía. Medellín, Colombia: Secretaría de Gobierno Municipal; 2007.
31. US Census Bureau. Statistical Abstract of the United States, 2004–2005. Washington, DC: Bureau of the Census, US Department of Commerce; 2005. ( http://www.census.gov/prod/www/abs/statab2001_2005.html). (Accessed May 8, 2011)
32. Creative Urban Projects. The Gondola Project: A Cable-Propelled Transit Primer. Toronto, Ontario, Canada: Creative Urban Projects; 2010. ( http://www.gondolaproject.com/2010/03/11/medellincaracas-part-1/). (Accessed May 8, 2011)
33. Medellíninfo.com. Metrocable. Brandon, FL: Waterfront Realty, Inc; 2011. ( http://www.medellininfo.com/metro/metrocable.html). (Accessed May 8, 2011)
34. Duque Ramírez L. La Violencia en el Valle de Aburrá: su Magnitud y Programa para Reducirla. (Universidad de Antioquia y Área Metropolitana del Valle de Aburrá) Medellín, Colombia: Fotográficas Mario Salazar; 2005.
35. Afifi A, Clark V. Cluster analysis. In: Afifi A, Clark V, editors. Computer-aided Multivariate Analysis. Boca Raton, FL: CRC Press; 1997. pp. 417–443.
36. Hansen B, Bowers J. Covariate balance in simple, stratified and clustered comparative studies. Stat Sci. 2008;23(2):219–236.
37. Hansen B, Olsen Klopfer S. Optimal full matching and related designs via network flows. J Comput Graph Stat. 2006;15(3):609–627.
38. Firth D. Bias reduction of maximum likelihood estimates. Biometrika. 1993;80:27–38.
39. Gail MH, Tan WY, Piantadosi S. Tests for no treatment effect in randomized clinical trials. Biometrika. 1988;75:57–64.
40. Rosenbaum P. Interference between units in randomized experiments. J Am Stat Assoc. 2007;102(477):191–200.
41. Sobel EM. What do randomized studies of housing mobility demonstrate?: causal inference in the face of interference. J Am Stat Assoc. 2006;101(476):1398–1407.
42. Rosenbaum P. Observational Studies. 2nd ed. New York, NY: Springer-Verlag New York; 2002.
43. Diez Roux AV. Neighborhoods and health: where are we and where do we go from here? Rev Epidemiol Sante Publique. 2007;55(1):13–21. [PMC free article] [PubMed]
44. Sampson RJ. Transcending tradition: new directions in community research, Chicago style. Criminology. 2002;40(2):213–230.
45. Oakes JM. The (mis)estimation of neighborhood effects: causal inference for a practicable social epidemiology. Soc Sci Med. 2004;58(10):1929–1952. [PubMed]
46. Durlauf SN, Nagin DS. Overview of “Imprisonment and crime: can both be reduced?” Criminol Public Policy. 2011;10(1):9–12.

Articles from American Journal of Epidemiology are provided here courtesy of Oxford University Press
PubReader format: click here to try


Related citations in PubMed

See reviews...See all...


  • MedGen
    Related information in MedGen
  • PubMed
    PubMed citations for these articles

Recent Activity

Your browsing activity is empty.

Activity recording is turned off.

Turn recording back on

See more...