Abstract
Objectives
Drawing from lifestyle-routine activity and self-control perspectives, the causal mechanisms responsible for repeat victimization are explored. Specifically, the present study investigates: (1) the extent to which self-control influences the changes victims make to their risky lifestyles following victimization, and (2) whether the failure to make such changes predicts repeat victimization.
Methods
Two waves of panel data from the Gang Resistance Education and Training program are used (N = 1,370) and direct measures of change to various risky lifestyles are included. Two-stage maximum likelihood models are estimated to explore the effects of self-control and changes in risky lifestyles on repeat victimization for a subsample of victims (n = 521).
Results
Self-control significantly influences whether victims make changes to their risky lifestyles post-victimization, and these changes in risky lifestyles determine whether victims are repeatedly victimized. These changes in risky lifestyles are also found to fully mediate the effects of self-control on repeat victimization.
Conclusions
Findings suggest that future research should continue to measure directly the intervening mechanisms between self-control and negative life outcomes, and to conceptualize lifestyles-routine activities as dynamic processes.
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Notes
Schreck’s (1999) argument could be viewed as an integration of the common dichotomy of heterogeneity versus state dependence explanations of victimization (see Lauritsen and Quinet 1995; Tseloni and Pease 2003; Wittebrood and Nieuwbeerta 2000). And although choosing one set of labels over another is somewhat arbitrary (Nagin and Paternoster 2000), we find Schreck’s use of the terms self-control and opportunity to simply be more useful in the present context because it is more consistent with the broader literature on victimization and repeat victimization.
Sample demographic characteristics of age, gender, and race are distributed similarly across all six cities. On average, however, respondents in Portland were slightly younger and Philadelphia contained a higher proportion of Black respondents relative to other cities. Principal investigators caution that these data are not a random subsection of adolescents. For a more detailed description of the GREAT program’s methodology and data collection procedures, see Esbensen et al. (2001).
As some may argue, a young adolescent sample may not be ideal to study the changes victims make to their lifestyles post-victimization. We recognize that such youths likely have less opportunity to restructure their behavioral routines than do older teenagers or adults. Nevertheless, a sufficient degree of variation is present across all measures of lifestyle changes from time 1 to time 2, and patterns involving self-control, changes in risky lifestyles, and repeat victimization occur in theoretically expected directions. Like others who have used the GREAT data to test general theoretical propositions involving self-control and victimization before us (e.g., Agnew et al. 2011; Jennings et al. 2010; Schreck et al. 2006), we deem our use of these data appropriate but recognize that we may be providing a conservative test of theory, since youth are unlikely to possess boundless autonomy.
Cases without complete victimization information at time 1 and time 2 were excluded in addition to cases containing implausible or extreme responses. Missing data due to item nonresponse on other key variables were handled using the multiple imputation suite (mi impute) available in Stata 12.0 (m = 20 imputations). Multiple imputation is a well-established approach to dealing with missing data (Acock 2005; Allison, 2000; Carlin et al. 2008; Rubin 1987; Schafer 1997), and the imputation model was specified using all variables in the present study (Royston 2004). Prior to imputation, approximately 1.82 percent of the 79,460 cells in the data file used in the present study contained missing values. Imputing the data allowed us to retain approximately 23 percent of our sample that would have otherwise been eliminated via listwise deletion. It is important to note that previous studies have reported that individuals lost after wave one in the GREAT data demonstrate higher levels of victimization and delinquency than those who participated in later waves (Agnew et al. 2011; Schreck et al. 2006), and that item nonresponse rates in the GREAT dataset have been shown to be higher among those with lower levels of self-control (Watkins and Melde, 2007). As a result, the findings reported below may represent conservative estimates since variation in the “tails” of the distributions of key variables of interest—which may otherwise serve to inflate the relationships of theoretical interest (particularly the relationships surrounding victimization, self-control, and risky lifestyles)—has been somewhat truncated. In using the imputed data, however, the possibility of making such an inferential error is minimized considerably over simple listwise deletion methods for missing values.
We recognize that other forms of non-violent victimization (e.g., theft) are also relevant to the study of repeat victimization (Averdijk and Loeber 2012; Farrell et al. 1995; Tseloni and Pease 2003). Although no victimization experience is trivial, in the present study we focus solely on violent, interpersonal victimization, and specifically on those types of violence that are associated with participation in risky lifestyles (Schreck et al. 2006; Stewart et al. 2004). Given the severity of violent victimization (MacMillan 2001), we are justified in assuming that many victims will feel compelled to make lifestyle changes to try and avoid being victimized again in the future.
Repeat victimization was measured dichotomously (1 = victimized again, 0 = not victimized again) in supplemental analyses, and the pattern of findings remained similar. We present analyses using a continuous measure of victimization since dichotomizing a continuous variable is typically only appropriate when the distribution of that variable is highly skewed (Irwin & McClelland, 2003; Streiner 2002). Indeed, the distribution of repeat victimization is relatively normal among the victim subsample (skew = .84; kurtosis = 2.20), and transforming it to a binary scheme would run the risk of losing important information on our outcome of interest.
Residual change scores are calculated rather than raw change scores (D = Y – X) to produce more reliable indicators of change from Time 1 to Time 2. As Cronbach and Furby (1970: 74) note, “Residualizing removes from the posttest score…the portion that could have been predicted linearly from pretest status.” Furthermore, Cronbach and Furby (1970: 74) go on to detail that “the residualized score is primarily a way of singling out individuals who changed more (or less) than expected,” indicating that these scores are well-suited for carrying out our research objectives.
The range in values for each residual change variable produced among the subsample of victims is as follows: change in risky socializing (3.99–9.16); change in substance use (.44–2.95); change in violence (.41–2.20); change in violent friends (1.27–2.08).
For an extensive review of empirical studies on the overlap between victimization and offending, see Jennings et al. (2012).
Routine activity theory suggests that the most convenient, visible, and accessible targets for crime are individuals with whom one spends time (Felson and Boba 2010). The same construct was included as an indicator of risky lifestyles specified by Schreck et al. (2006), and we also deem it as an important and theoretically-relevant indicator to include in the present examination (see also Lauritsen et al. 1992; Schreck et al. 2002).
A potential drawback of the GREAT data is that it relies on students’ knowledge of their friends’ violent behaviors. Research has demonstrated that respondents’ perceptions of peer delinquency may be biased to a certain extent by hearsay or by the likelihood of individuals to project their own tendencies onto their friends (Haynie and Osgood 2005; Weerman and Smeenk 2005; Young et al. 2011). Nevertheless, respondent-generated peer measures remain common when investigating peer violence in both criminological and victimization research (Lauritsen et al. 1992; Pratt et al. 2010; Schreck et al. 2002), and our finding that those with low self-control continue to maintain friendships with violent peers post-victimization is consistent with theoretical expectations. Even so, we recognize a potential inferential risk when using such measures (Gottfredson and Hirschi 1987). To examine in greater detail the impact of victimization on violent peer groups—a focus well beyond that of the present examination—researchers may wish to use network data from other sources such as the National Longitudinal Study of Adolescent Health (Add Health).
These patterns are unlikely to be unique to these particular variables, but rather likely reflect the more “general” trend of reduced magnitude of the effects of variables from cross-sectional to longitudinal research designs (see the discussion by Moffitt 1993).
Different types of selection necessitate different model specifications and statistical estimators. If selection into the subsample is explicit or random, we would not expect selection bias to be an issue, and a simple two-part model (or an “uncorrected model”) would be the appropriate modeling strategy (Bushway et al. 2007; Duan et al. 1984). In the present study, however, selection into the victim subsample is incidental and potentially non-random. Accordingly, changes to risky lifestyles and repeat victimization are likely conditional on being selected into the victim subsample, and these issues are taken into account with our modeling strategy.
Following the recommendations of Bushway and colleagues (2007), we compared maximum likelihood estimates with those provided by simple two-part models (for all outcomes) and with Heckman’s two-step correction (for changes in risky lifestyles). Heckman’s two-step estimator involves the estimation of a probit model for selection, and then calculates an inverse Mills ratio that is inserted into a second OLS model of interest (Heckman 1976). Alternatively, in a simple two-part model, no correction is inserted and no additional technique is required—models are simply estimated one after the other, with the assumption that random selection into the subsample occurred (Duan et al. 1984). In comparing estimates across these various methods, standard errors were notably inconsistent. To ensure our estimates are as unbiased and efficient as possible, we report results from the FIML models. As Bushway and colleagues (2007: 159) point out, “when the error assumptions are met the FIML will always be more efficient than the Heckman two-step, a fact which has been demonstrated in numerous simulation studies” (see also Leung and Yu 1996; Puhani 2000).
Clustered robust standard errors are intended to make the standard errors robust to both serial correlation (due to the non-independence of observations within clusters) and to heteroskedasticity (due to differing variance estimates emerging from the observations between clusters) without having to make any assumptions about the functional form of either (Rogers 1993; Wooldridge 2009).
A review of existing Monte Carlo studies suggests that the FIML is more efficient if the collinearity between the inverse Mills ratio (calculated from the stage 1 equation) and the other regressors is moderate (Puhani 2000). Results from regressing the inverse Mills ratio on independent variables for lifestyle change equations revealed that exclusion restrictions are appropriate (R 2 < .45), and condition indices are low. Puhani (2000) argued that situations where condition numbers exceed 20 and where collinearity is problematic are those in which simple two-part models should be estimated. If there are no collinearity problems, however, the FIML estimator is recommended and appropriate.
As mentioned above, each dependent variable in Models 2 through 5 represents a residual change score. To clarify the interpretation of these change scores, positive, larger values on the change variables represent larger residuals, which reflect less change from time 1 to time 2.
In simple two-part models the standard errors were notably lower and coefficients were inflated, although the broad pattern of results remained the same as we present here.
A series of diagnostic tests similar to those described previously were first conducted to ensure that the models estimated to test for robustness were not biased due to collinearity. Condition indices were below 20 in all of the models specified, and VIF scores did not exceed 2.80. Collinearity issues prevented the inclusion of changes in violence and changes in violent friends as independent variables in the same model.
It is worth noting that scholars who have struggled to disentangle the relationship between self-control and repeat victimization in prior work have been hesitant to make suggestions for victim support services, since the direct mechanisms through which self-control influences victimization were not yet made clear. Until the present study, it seemed that efforts to reduce victimization would have the greatest hope of success if they could proactively instill self-control in young children (see e.g., Schreck et al. 2002, 2006). Given our findings, it is clear that victim-prevention efforts should help victims change their problematic routine activities through responsive programming, rather than change their levels of self-control—a much more feasible and practical solution to preventing repeat victimization (Lauritsen and Archakova 2008; Piquero et al. 2010).
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The authors are grateful to Michael D. Reisig and Mario V. Cano for their helpful comments and suggestions.
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Turanovic, J.J., Pratt, T.C. “Can’t Stop, Won’t Stop”: Self-Control, Risky Lifestyles, and Repeat Victimization. J Quant Criminol 30, 29–56 (2014). https://doi.org/10.1007/s10940-012-9188-4
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DOI: https://doi.org/10.1007/s10940-012-9188-4