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The Impact of Imprisonment on Marriage and Divorce: A Risk Set Matching Approach

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Abstract

Marriage has a prominent place in criminological theory and research as one institution that has the potential to genuinely foster desistance from a criminal career. Mass imprisonment policies in the United States and elsewhere, therefore, pose a potential threat of increased crime if they impede the ability of ex-prisoners to reintegrate into society by stigmatizing them and limiting their chances in the marriage market. We use a long-term study of a conviction cohort in The Netherlands to ascertain the effect that first-time imprisonment has on the likelihood of marriage and divorce. The results suggest that the effect of imprisonment on the likelihood of marriage (among unmarried offenders) is largely a selection artifact, although there is very weak evidence for a short-lived impact that does not persist past the first year post-release. This is interpreted as a residual incapacitation effect. On the other hand, the results strongly suggest that the experience of incarceration leads to a substantially higher divorce risk among offenders who are married when they enter prison.

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Notes

  1. For example, Blokland and Nieuwbeerta (2005); Farrington and West (1995); Horney et al. (1995); King et al. (2007); Laub et al. (1998); Laub and Sampson (2003); Ouimet and LeBlanc (1996); Piquero et al. (2002); Sampson and Laub (1990, 1993); Sampson et al. (2006); Shover (1996); Warr (1998). These studies rely heavily on samples that are considerably high risk, for example, Piquero et al.’s (2002) prospective analysis from a sample of serious male offenders released from the California Youth Authority. For a much more qualified perspective on the salience of marriage, see Giordano et al. (2002, 2007).

  2. In the Dutch criminal justice system, the public prosecutor has the discretionary power not to prosecute every case forwarded by the police. The public prosecutor may decide to drop the case if prosecution would probably not lead to conviction due to lack of evidence or for technical considerations (e.g., procedural or technical waiver). The public prosecutor is also authorized to waive prosecution “for reasons of public interest” (i.e., waiver for policy considerations). The Board of Prosecutors-General has issued national prosecution guidelines under which a public prosecutor may decide to waive a case for policy reasons, for example, if measures other than penal sanctions are preferable or more effective, prosecution would be disproportionately unjust or ineffective in relation to the nature of the offense or the offender, or prosecution would be contrary to the interest of the state or the victim (Tak 2003).

  3. Note that in The Netherlands, a person is not given a “clean slate” upon becoming an adult. The extracts used thus contain information on both juvenile and adult offenses.

  4. While the penal regime in The Netherlands has become harsher over the years, still more than 80% of the unsuspended custodial sanctions imposed in 2007 (the most recent figure available from Statistics Netherland) were shorter than 12 months. Similar percentages have been reported in many other European countries such as Belgium, Denmark, Finland, France, Italy, Norway, Sweden, and Switzerland (see Aebi et al. 2006).

  5. In the present context, “treatment” is generically taken to mean any intentional intervention. It is not to be confused with participation in a correctional rehabilitation program.

  6. Propensity score matching is similar to standard regression in that it is assumed in both cases that selection into treatment is random conditional on observed characteristics. However, propensity score matching differs from regression in at least two key ways. First, it does not rely on a linear functional form to estimate treatment effects. Although the propensity score is estimated using a parametric model, once obtained, individuals are matched non-parametrically. Second, propensity score matching highlights the issue of common support by revealing the degree to which untreated cases resemble the treated cases on observed characteristics. Standard regression (a.k.a. covariate adjustment), on the other hand, obscures this issue and risks extrapolating treatment effect estimates based solely on functional form when treated and untreated groups are actually incomparable. In many applications, only a subset of the untreated population (and perhaps the treated population as well) will be useful for estimating treatment effects. For recent empirical work employing propensity score matching, see Morgan (2001) and Harding (2003).

  7. Risk set matching is only one technique that allows the propensity score to vary as a function of age- or time-dependent covariates, a recent application of which is provided by Lu (2005). A similar goal is achieved by inverse probability-of-treatment weighting (IPTW), which is in the class of marginal structural models discussed by Robins (1999) and Robins et al. (2000). For a recent application of this approach, see Sampson et al. (2006).

  8. The underlying rationale for this approach is well argued by Li et al. (2001) in their hypothetical example of a clinical trial:

    Imagine a strict rule that assigned patients to treatment whenever their symptoms became acute. In this hypothetical case, to know that a patient never received treatment is to know that the patient had a relatively favorable outcome. If the control group consisted of all patients who never received treatment, then it would contain only patients with favorable outcomes, because any patient whose symptoms later became acute received the treatment. (Li et al., 2001, p. 871)

    Simply put, untreated subjects in this hypothetical scenario were never truly at risk of being treated. In the language of program evaluation, treatment is not independent of potential outcomes. Such an after-the-fact selection rule would obviously introduce extreme biases into any treatment effect estimates.

  9. We employed a wide range of matching protocols and achieved results that were substantially similar. The results we display are from 1-to-1 matching with replacement and a caliper of 0.001. In sensitivity analyses, we matched each treated individual with one, three, and five nearest neighbors within calipers of 0.05, 0.01, and 0.001.

  10. As the formula shows, the standardized difference provides an estimate of the mean difference as a proportion of the average standard deviation. Rosenbaum and Rubin (1985) proposed using the standardized difference to judge covariate balance before and after matching on the propensity score, which we do in the appendix. However, the measure also has utility for estimating an effect size for the average treatment effect.

  11. The transformation, exp(b) − 1, provides the proportional increase/decrease in the hazard of imprisonment given a one-unit increase in the explanatory variable, evaluated at the means of the remaining covariates.

  12. Note that the hazard model is estimated for the entire eligible sample (i.e., individuals convicted at age t with no previous incarceration spell), including those who are married as well as unmarried at the time of their conviction/incarceration. We control for marital status at the time of conviction in the model. We pool both samples together in the propensity score model because there is no reason to believe that the incarceration mechanism differs qualitatively for married and unmarried men. Then, in order to estimate the average treatment effect (ATE) of incarceration, we stratify the sample directly by the offender’s marital status. The strategy of estimation within subpopulations defined by the covariates has precedence in the literature on the propensity score methodology (Rosenbaum and Rubin 1984).

  13. Note that most of the offenses labeled as attempted manslaughter in The Netherlands would be classified as assaults in the US.

  14. Comparing the covariates listed in Table 1 for the treated and untreated before and after conditioning on the propensity score shows that, before matching, there is imbalance on a number of covariates. In particular, using mean comparisons (t-tests) about half of the covariates are imbalanced, while using effect sizes about one-quarter are imbalanced. After matching, however, there is (almost) complete balance. Details on covariate balance are provided in the appendix.

  15. Imprisoned men for whom we were unsuccessful in identifying suitable matches tended to be convicted of comparatively more serious offenses and to have a more extensive criminal history. For example, they were more likely to be convicted of rape or violent theft, to have more crimes involved in their conviction offense, and to have more prior property convictions.

  16. The imprisoned men who were off support were more likely to be convicted of violent offenses (e.g., rape, violent theft, aggravated assault) and less likely to be convicted of property offenses (e.g., theft, forgery, weapons act), had a higher offense severity score and more extensive criminal histories, and were convicted for the first time prior to age 16. They were also more likely to be ethnic minorities.

  17. Results are not shown but are available upon request.

  18. Interestingly, the effect of children appears to be opposite (but not quite marginally so) for convicted but non-imprisoned men: Convicted men with children have a divorce probability of 0.21 compared to 0.11 among convicted men without children (p < .107).

  19. To conduct the analysis, we invoke the user-written Stata routine—mhbounds—developed by Becker and Caliendo (2007).

  20. It important to emphasize that this sensitivity analysis generates “worst case” bounds on estimated treatment effects. That is, even small values of Γ that result in non-significance of a treatment effect do not invalidate the original estimates. DiPrete and Gangl (2004) explain that non-significance simply means that confidence intervals for the impact of incarceration would include zero if an unobserved variable was responsible for a difference in the odds of treatment assignment between imprisoned and non-imprisoned individuals, and “if this variable’s effect on [marriage or divorce] was so strong as to almost perfectly determine whether [the likelihood of marriage or divorce] would be bigger [or smaller] for the treatment or the control case in each pair of matched cases in the data” (DiPrete and Gangl 2004, p. 291, emphasis removed). They explain further that, in instances where unobserved confounding strongly affects treatment assignment but only weakly influences the response variable, the estimated confidence intervals would not include zero. We would add further that, if the unobserved variable is not binary, then the Rosenbaum bounds are again too wide for a given value of Γ.

  21. If we instead estimate Rosenbaum bounds on the 1-year marriage likelihood, we find that positive self-selection on the order of Γ = 1.05 pushes the incarceration effect on marriage to 10-percent significance, while Γ = 1.15 pushes it to 5-percent significance.

  22. This is not a universal sentiment, however. There remains some evidence that imprisonment can have a substantial deterrent effect on criminal behavior (e.g., Bhati and Piquero 2008).

  23. The underlying causal mechanism is not necessarily attributable to the signal that such confinement sends about an offender’s risk for domestic violence, however, since the divorce likelihood does not vary by offense severity among convicted men. It is quite possible that this is an artifact of sentence length. Simply put, serious offenders serve longer terms of confinement and thus face lengthier time out from marriage, which can strain marital bonds.

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Acknowledgments

This paper was completed during the time that Robert Apel was a visiting scholar at The Netherlands Institute for the Study of Crime and Law Enforcement (NSCR). He is grateful to the institute for its hospitality and generous provision of resources. The authors are also thankful to Candace Kruttschnitt and Daniel Nagin, who offered feedback and provided invaluable discussion. The constructive comments of the co-Editor (Alex Piquero) and anonymous reviewers also greatly improved this article.

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Appendices

Appendix A

Details on the Estimation of Rosenbaum Bounds for the Average Treatment Effect of Incarceration on Marriage Formation and Stability

In this appendix, we elaborate on the logic and estimation of “Rosenbaum bounds” for the sensitivity of the average treatment effect (ATE) to hidden bias. Our description draws from Rosenbaum (2002), Becker and Caliendo (2007), and DiPrete and Gangl (2004). Our application involves estimation of the impact of incarceration on the likelihood of marriage and divorce. The sensitivity analysis begins with the formulation of the usual propensity score, but supplements the model with an additional, unobserved component:

$$ \pi = \Pr \left( {{\text{Inc}} = 1} \right) = {\frac{{\exp \left( {\alpha + \beta X + \gamma U} \right)}}{{1 + \exp \left( {\alpha + \beta X + \gamma U} \right)}}} $$

where X are the observed variables, U is an unobserved variable, and α, β, and γ are unknown parameters. Because our model conditions only on individuals who were convicted of a crime, we may conceive of U as some kind of “crime risk trait” that is observed by a sentencing judge but is unobserved by the researcher, and whose presence increases the probability of receiving a sentence of incarceration by a factor of γ. The familiar logit (log-odds) formulation of this model is represented as:

$$ \ln \left( {{\frac{\pi }{1 - \pi }}} \right) = \ln \left[ {{\frac{{\Pr \left( {{\text{Inc}} = 1} \right)}}{{1 - \Pr \left( {{\text{Inc}} = 1} \right)}}}} \right] = \alpha + \beta X + \gamma U $$

and exponentiation leaves us with the odds of incarceration for an arbitrary individual in the sample:

$$ {\frac{\pi }{1 - \pi }} = {\frac{{\Pr \left( {{\text{Inc}} = 1} \right)}}{{1 - \Pr \left( {{\text{Inc}} = 1} \right)}}} = \exp \left( {\alpha + \beta X + \gamma U} \right) $$

If there is hidden bias or unobserved confounding, two paired individuals i and j with the same observed covariates X (or the same propensity score) still have different chances of being incarcerated. The problem can be illustrated by taking the ratio of the odds of treatment for these two individuals:

$$ {\frac{{{{\pi_{i} } \mathord{\left/ {\vphantom {{\pi_{i} } {\left( {1 - \pi_{i} } \right)}}} \right. \kern-\nulldelimiterspace} {\left( {1 - \pi_{i} } \right)}}}}{{{{\pi_{j} } \mathord{\left/ {\vphantom {{\pi_{j} } {\left( {1 - \pi_{j} } \right)}}} \right. \kern-\nulldelimiterspace} {\left( {1 - \pi_{j} } \right)}}}}} = {\frac{{\exp \left( {\alpha + \beta X_{i} + \gamma U_{i} } \right)}}{{\exp \left( {\alpha + \beta X_{j} + \gamma U_{j} } \right)}}} $$

where i indexes an incarcerated (treated) individual and j indexes a non-incarcerated (untreated) individual. Because the propensity score balances X, this odds ratio (or odds multiplier) can be algebraically simplified:

$$ {\frac{{\exp \left( {\gamma U_{i} } \right)}}{{\exp \left( {\gamma U_{j} } \right)}}} = \exp \left[ {\gamma \left( {U_{i} - U_{j} } \right)} \right] $$

A study is free of unobserved confounding only if there are no differences in unobservables (i.e., U i  = U j for all matched pairs i,j), or the unobservables do not influence the probability of incarceration (i.e., γ = 0). In the absence of direct information on the unobservables, however, Rosenbaum (2002) proposes a simulation that subjects γ to perturbations as a way to assess its influence on treatment effect estimates. In order to make the sensitivity analysis tractable, we can impose the simplifying assumption that U is a dummy variable, that is, it is either present or absent. This implies the following bounds on the odds ratio that either of two individuals matched on X will be incarcerated:

$$ {\frac{1}{\Upgamma }} \le {\frac{{{{\pi_{i} } \mathord{\left/ {\vphantom {{\pi_{i} } {\left( {1 - \pi_{i} } \right)}}} \right. \kern-\nulldelimiterspace} {\left( {1 - \pi_{i} } \right)}}}}{{{{\pi_{j} } \mathord{\left/ {\vphantom {{\pi_{j} } {\left( {1 - \pi_{j} } \right)}}} \right. \kern-\nulldelimiterspace} {\left( {1 - \pi_{j} } \right)}}}}} \le \Upgamma $$

where

$$ \Upgamma = \exp \left( \gamma \right) $$

A number of sensitivity statistics are available for matching estimators depending on the distribution of the response variable and the matching procedure used (for review, see Rosenbaum 2002). With a binary outcome and one nearest neighbor, we employ Mantel and Haenszel (1959) test statistic. This is a non-parametric test that compares the observed number of incarcerated (treated) men that are married (or divorced) to the expected number given that the treatment effect is zero. We adapt the notation of Becker and Caliendo (2007) to our particular application:

$$ Q_{\text{MH}} = {\frac{{\left| {Y_{1} - \sum_{s = 1}^{S} E\left( {Y_{1s} } \right)} \right| - 0.5}}{{\sqrt {\sum_{s = 1}^{S} {\text{Var}}\left( {Y_{1s} } \right)} }}} = {\frac{{\left| {Y_{1} - \sum\limits_{s = 1}^{S} {\left( {{\frac{{N_{1s} Y_{s} }}{{N_{s} }}}} \right)} } \right| - 0.5}}{{\sqrt {\sum\limits_{s = 1}^{S} {\left( {{\frac{{N_{1s} N_{0s} Y_{s} \left( {N_{s} - Y_{s} } \right)}}{{N_{s}^{2} \left( {N_{s} - 1} \right)}}}} \right)} } }}} $$

where s represents a single stratum (s = 1,2,…,S) or, in our case, a single matched set and

  • Y1 = the total number of imprisoned or treated individuals in the sample who are married (divorced).

  • Y1s  = the total number of imprisoned individuals in matched set s who are married (divorced).

  • Y s  = the total number of individuals in matched set s who are married (divorced).

  • N1s  = the number of imprisoned individuals in matched set s (=1 in our study).

  • N0s  = the number of non-imprisoned individuals in matched set s (=1 in our study).

  • N s  = the number of individuals in matched set s.

For fixed Γ ≥ 1.0 and U ∈ {0,1}, results shown in Rosenbaum (2002) demonstrate that Q MH can be bounded by two known distributions, providing an upper and lower bound. Using notation from Becker and Caliendo (2007), the upper and lower bounds, respectively, are given by:

$$ Q_{\text{MH}}^{ + } = {\frac{{\left| {Y_{1} - \sum_{s = 1}^{S} \tilde{E}_{s}^{ + } } \right| - 0.5}}{{\sqrt {\sum_{s = 1}^{S} {\text{Var}}\left( {\tilde{E}_{s}^{ + } } \right)} }}} $$

and

$$ Q_{\text{MH}}^{ - } = {\frac{{\left| {Y_{1} - \sum_{s = 1}^{S} \tilde{E}_{s}^{ - } } \right| - 0.5}}{{\sqrt {\sum_{s = 1}^{S} {\text{Var}}\left( {\tilde{E}_{s}^{ - } } \right)} }}} $$

with details on the large-sample approximations of \( \tilde{E}_{s}^{ + } \) and \( {\text{Var}}\left( {\tilde{E}_{s}^{ + } } \right) \), as well as \( \tilde{E}_{s}^{ - } \) and \( {\text{Var}}\left( {\tilde{E}_{s}^{ - } } \right) \), given in Becker and Caliendo (2007, p. 74, note 5).

Appendix B

See Table 5.

Table 5 Balance diagnostics for imprisoned and non-imprisoned offenders, full and matched samples

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Apel, R., Blokland, A.A.J., Nieuwbeerta, P. et al. The Impact of Imprisonment on Marriage and Divorce: A Risk Set Matching Approach. J Quant Criminol 26, 269–300 (2010). https://doi.org/10.1007/s10940-009-9087-5

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