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Deterring Gang-Involved Gun Violence: Measuring the Impact of Boston’s Operation Ceasefire on Street Gang Behavior

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Abstract

Objectives

The relatively weak quasi-experimental evaluation design of the original Boston Operation Ceasefire left some uncertainty about the size of the program’s effect on Boston gang violence in the 1990s and did not provide any direct evidence that Boston gangs subjected to the Ceasefire intervention actually changed their offending behaviors. Given the policy influence of the Boston Ceasefire experience, a closer examination of the intervention’s direct effects on street gang violence is needed.

Methods

A more rigorous quasi-experimental evaluation of a reconstituted Boston Ceasefire program used propensity score matching techniques to develop matched treatment gangs and comparison gangs. Growth-curve regression models were then used to estimate the impact of Ceasefire on gun violence trends for the treatment gangs relative to comparisons gangs.

Results

This quasi-experimental evaluation revealed that total shootings involving Boston gangs subjected to the Operation Ceasefire treatment were reduced by a statistically-significant 31 % when compared to total shootings involving matched comparison Boston gangs. Supplementary analyses found that the timing of gun violence reductions for treatment gangs followed the application of the Ceasefire treatment.

Conclusions

This evaluation provides some much needed evidence on street gang behavioral change that was lacking in the original Ceasefire evaluation. A growing body of scientific evidence suggests that jurisdictions should adopt focused deterrence strategies to control street gang violence problems.

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Notes

  1. Wright et al. (2004, p. 184) offer a clever metaphor of this perspective: “A restaurant owner can sell more prime rib by lowering its price, but not to vegetarian patrons. The price of prime rib here represents the situational inducement toward ordering meat, but vegetarianism represents a predisposition away from it, and thus the effect of meat pricing significantly varies by level of meat eating.”

  2. See Massachusetts General Laws, Chapter 265, Section 15A.

  3. We used data from a recent social network analysis of the rivalries and alliances among Boston gangs to identify the untreated gangs that were socially connected to the N = 19 Ceasefire gangs. Rivalries and alliances between gangs were determined through focus groups with police officers, probation officers, and streetworkers (city-employed gang outreach workers) based on their working knowledge of past and ongoing gang violence. Some gangs connected in rivalries and alliances to Ceasefire gangs also directly received treatment. For instance, the Lucerne Street Doggz had rivalries with eight other gangs and alliances with four other gangs. During the study period, three of their rivals (Castlegate, Morse, and Norfolk) and three of their allies (Favre, Kaos, and Orchard Park) also experienced Ceasefire interventions. N = 22 untreated gangs directly connected to Ceasefire gangs via rivalries or alliances were excluded from consideration for inclusion in our quasi-experimental design. The exercise resulted N = 82 gangs as possible comparison groups (123 total gangs—19 treated gangs—22 untreated gangs that were socially connected to treated gangs = 82 possible comparison gangs).

  4. Gang membership size was calculated from the roster of members of each gang in the BPD BRIC’s gang intelligence database.

  5. We used ArcGIS 10.0 mapping software to map the turf of Boston gangs as polygons that occupied a circumscribed amount of space. We created a matrix of turf adjacency where a tie occurs if any side of a gang polygon touches at least one side of another gang polygon.

  6. Longevity was determined by comparing the roster of N = 123 gangs with at least one shooting during the 2006–2010 study time period to the roster of active Boston gangs in 1995 identified by Kennedy et al. (1997).

  7. The concentrated disadvantage index is a standardized index composed of the percentage of residents who are black, the percentage of residents receiving public assistance, the percentage of families living below the poverty line, the percentage of female-headed households with children under the age of 18, and the percentage of unemployed residents (as measured by the percentage of men over the age 16 who did not work in the previous year) (see Morenoff et al. 2001; Sampson et al. 1997). Because of the high correlation of these variables, we conducted principal components factor analysis, which revealed that variables load on a single factor (which was retained as a standardized index variable). For example, a Boston block group featuring a disadvantage index score of 1.5 would be 1.5 SD more disadvantaged than the mean Boston block group. As such, the disadvantage index is adjusted specifically for the city of Boston using 2000 Census variables, even while the components used to construct the index remain constant across much neighborhood research and remain robust predictors of crime across a variety of city types and spatial aggregations. For those gangs whose turf spanned more than one census block group, we used a spatially-weighted mean of the connected block groups to calculate the disadvantaged index for the neighborhood surrounding each gang’s turf.

  8. For balancing properties to be satisfied in the propensity score matching analysis, certain pre-treatment characteristics needed to be entered as dummy variables into the Stata 12.0 PSMATCH2 routine. The total number of shootings in 2006 and the number of members of each gang were entered as interval-level measures. Adjacent gang turf was coded “0” for gangs that did not have turf adjacent to another gang’s turf and “1” for gangs that did have turf adjacent to another gang’s turf. Longevity was coded “0” for gangs that did not exist in 1995 and “1” for gangs that did exist in 1995. The number of rivalries was coded as “0” for gangs that had 2 or fewer rivalries and “1” for gangs that had 3 or more rivalries. The number of alliances was coded as “0” for gangs that had no alliances and “1” for gangs that had alliances with at least one other gang. Housing project gang was coded as “0” for gangs not located in a housing project and “1” for gangs were located in a housing project. The concentration of disadvantage in the surrounding Census block group(s) was coded as “0” for gang turf located in block groups below the 75th percentile and “1” for gang turf located in block groups at the 75th percentile or greater. The number of gang arrests in 2006 was coded as “0” for gangs with 14 or fewer arrests in 2006 and “1” for gangs with 15 or more arrests in 2006.

  9. The quarterly total gang-involved shootings for the N = 53 treatment and comparison gangs used in these analyses were distributed as overdispersed count data. The distribution had a mean = 1.39, standard deviation = 1.89, and variance = 3.57. One sample Kolmogorov–Smirnov nonparametric tests rejected the null hypotheses that the observed distribution was not different from a normal distribution (p < 0.0001) and not different from a Poisson distribution (p < 0.0001).

  10. Quarter 1 served as the reference category for this polychotomous dummy variable. Quarter 1 represented whether the outcome included the sum of January, February, and March shootings (1 = Yes, 0 = No). Quarter 2 represented whether the outcome included the sum of April, May, and June shootings (1 = Yes, 0 = No). Quarter 3 represented whether the outcome included the sum of July, August, and September shootings (1 = Yes, 0 = No). Quarter 4 represented whether the outcome included the sum of October, November, and December shootings (1 = Yes, 0 = No).

  11. http://gemini.gmu.edu/cebcp/EffectSizeCalculator/d/mean-gains-scores-and-gain-score.html.

  12. Since the selection of a matching algorithm and its particular specification can be a subjective process (Apel and Sweeten 2010), we conducted a supplementary analysis to ensure that any program impacts were robust across a variety of matching algorithms and caliper/bandwidth selections. This exercise was not intended to be an exhaustive examination of all possible propensity score methods. As such, we included a representative selection of approaches: radius matching (calipers = 0.1, 0.01, 0.001), Gaussian kernel matching (bandwidth = 0.1, 0.01, 0.001), Epanechnikov kernel matching (bandwidth = 0.1, 0.01, 0.001), stratification matching (10 strata), and simple nearest neighbor matching. While the estimates differed somewhat across the varying propensity score matching methods, the Ceasefire treatment effect remained robust. The Ceasefire impact estimates ranged from a statistically significant 28 % reduction (p < 0.05) to a statistically significant 35 % reduction (p < 0.05).

  13. A value of Γ = 1.45 for total gang shootings indicates that the confidence interval for the Ceasefire treatment effect would include zero if an unobserved variable caused the chance of treatment assignment to differ between treatment and control groups by 1.45 and if this variable’s effect on total shootings was so strong as to almost perfectly determine whether total shootings would be bigger for the treatment or the control gang in each pair of matched gangs in the data (see DiPrete and Gangl 2004).

  14. Similar conclusions can be drawn by comparing the Rosenbaum bounds results to the ATT models for 2010 suspect shootings (ATT = −3.54, SE = 1.73, p < 0.05) and 2010 victim shootings (ATT = −2.11, SE = 1.24, p < 0.10). For all three ATT models (radius matching, caliper = 0.01), bootstrapped standard errors with 100 replications are provided.

  15. We excluded Quarter 1 and Quarter 20 to ensure that our quarterly impact estimates were based on at least two quarters (6 months) of shooting data for each Ceasefire gang.

  16. Using the Maryland Scientific Methods Scale (Sherman et al. 1997) as a standard, the original Ceasefire impact evaluation would be considered a “Level 3” evaluation and also regarded as the minimum design that is adequate for drawing conclusions about program effectiveness. This design rules out many threats to internal validity such as history, maturation/trends, instrumentation, testing, and mortality. However, as Farrington et al. (2002) observe, the main problems of Level 3 evaluations center on selection effects and regression to the mean due to the non-equivalence of treatment and control conditions. This evaluation of Ceasefire would be considered a “Level 4” evaluation as it measures outcomes before and after the program in multiple treatment and control condition units. These types of designs have better statistical control of extraneous influences on the outcome and, relative to lower level evaluations, deals with selection and regression threats more adequately.

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Authors and Affiliations

  1. Rutgers University, Newark, NJ, USA

    Anthony A. Braga

  2. John F. Kennedy School of Government, Harvard University, 79 John F. Kennedy Street, Cambridge, MA, 02138, USA

    Anthony A. Braga, David M. Hureau & Andrew V. Papachristos

  3. Yale University, New Haven, CT, USA

    Andrew V. Papachristos

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Braga, A.A., Hureau, D.M. & Papachristos, A.V. Deterring Gang-Involved Gun Violence: Measuring the Impact of Boston’s Operation Ceasefire on Street Gang Behavior. J Quant Criminol 30, 113–139 (2014). https://doi.org/10.1007/s10940-013-9198-x

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