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Assessing the Impact of First-Time Imprisonment on Offenders’ Subsequent Criminal Career Development: A Matched Samples Comparison

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Abstract

Using data from the Netherlands-based Criminal Career and Life-course Study the effect of first-time imprisonment between age 18–38 on the conviction rates in the 3 years immediately following the year of the imprisonment was examined. Unadjusted comparisons of those imprisoned and those not imprisoned will be biased because imprisonment is not meted out randomly. Selection processes will tend to make the imprisoned group disproportionately crime prone compared to the not imprisoned group. In this study group-based trajectory modeling was combined with risk set matching to balance a variety of measurable indicators of criminal propensity. Findings indicate that first-time imprisonment is associated with an increase in criminal activity in the 3 years following release. The effect of imprisonment is similar across offence types.

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Notes

  1. All cases ruled upon by a judge and all cases ‘dismissed for policy reasons’ or ‘dismissed for technical reasons’—for example due to failing evidence—by the Public Prosecutor.

  2. Note that in the Netherlands a person is not given a ‘blank sheet’ upon becoming an adult. The extracts used thus contain information on both juvenile and adult offenses.

  3. While the penal regime in the Netherlands has become harsher over the years, still more than 80% of the unsuspended custodial sanctions imposed in 1999 (most recent numbers available) were below 12 months. Similar percentages were found in many other European countries such as Belgium, Denmark, Finland, France, Italy, Norway, Sweden and Switzerland (WODC 2003).

  4. To estimate post-treatment yearly conviction rates taking into account the time offenders were ‘on the street’ and at risk of committing an offense, we calculated the conviction rates only over the period not incarcerated.

  5. While neither official nor self-report data provide a ‘true’ measure of an individual’s criminal behavior (Farrington 1986), we recognize that addressing issues of recidivism based on convictions might introduce bias. If prisons are indeed ‘schools of crime’ it could be the case that ex-prisoners actually commit more crimes than those not imprisoned, but that at the same time have better learned to go about undetected. The use of conviction data will then underrate the actual recidivism of the ex-prisoners thereby masking actual differences between the imprisoned and not imprisoned group. Thus, to the extent ex-prisoners learn to avoid detection more so than non-imprisoned, convictions may underestimate recidivism for ex-prisoners. On the other hand, the use of conviction data may also result in an overestimate of the treatment effects. Police may be more vigilant towards ex-prisoners and Public Prosecutors may be more inclined to press charges. Yet, given that the police are not always conscious of the adjudication of a particular criminal case, their vigilance is most probably triggered by knowing the offender, rather than his sentence. In addition note that in this study discretionary dismissals by the Public Prosecutor are also counted under convictions, thereby dispelling this possible source of bias at least at the Prosecutors level. It is impossible to judge the overall effects of these potential sources of bias but it is important to keep in mind that all measures of criminality including self reports suffer from comparably important sources of bias.

  6. A nontechnical survey of methods and results about propensity scores is given by Joffe and Rosenbaum (1999), and for several case-studies, see Rosenbaum and Rubin (1984, 1985), Smith (1997) and Dehejia and Wahba (1999).

  7. Note that since were are interested in the probability of imprisonment conditional on being convicted at time t, propensity score estimates are based on the 5,264 person-years—out of which 1,475 coded as ‘imprisoned’—in which people were convicted.

  8. The Dutch suspended sentence is a hybrid form of the Belgian-French sursis and the Anglo-Saxon probation. A suspended sentence means the non-implementation of an imposed sentence. A prison sentence up to 1 year may be suspended totally or in part. Prison sentences between 1 and 3 years may be suspended for a maximum of one-third of the total sentence. Prison sentences of over 3 years may not be suspended at all. Other community sanctions include electronic monitoring (Tak 2003).

  9. Specifically, the outcome estimates and their standard errors were calculated as follows: Let:

    \( T_{t} = {\frac{1}{{N_{t} }}}\sum\limits_{i}^{{N_{\text{t}} }} {\left[ {y_{\text{it}}^{\text{im}} - \left( {{\frac{1}{{n_{\text{i}} }}}\sum\limits_{j}^{{n_{\text{i}} }} {y_{\text{ijt}}^{\text{c}} } } \right)} \right]} \)

    where, i, an index of the ith imprisoned individual from a total set of N t individuals imprisoned in t; n i, the number of controls matched to the ith imprisoned individual; j, an index of the jth of the n i controls matched to i; \( y_{\text{it}}^{\text{im}} \), i’s conviction rate in the 3 year period immediately following t; \( y_{\text{ijt}}^{\text{c}} \), the conviction rate of the jth control matched to i in the 3 years period following i’s imprisonment in t; T t, estimated effect of imprisonment at age t.

    If n i were constant across i, T t could be estimated as the difference in the average of \( y_{\text{it}}^{\text{im}} \) and the average of \( y_{\text{ijt}}^{\text{c}} \). However, if ni is variable this “difference of the grand means” calculation is not correct. The correct calculation is the average of the individual differences between the imprisoned individual’s response and the average response of that treated individual’s matched controls.

    The variability of n i also must be taken into account in computing the standard error of T t. Assuming that \( y_{\text{it}}^{\text{im}} \) and\( y_{\text{ijt}}^{\text{c}} \), respectively have constant variances σm and σc, the standard error of the estimate Tt is \( {\frac{1}{{N_{\text{t}} }}}\left[ {\sum\limits_{i}^{{N_{\text{t}} }} {\left( {\sigma_{m}^{2} + {\frac{{\sigma_{c}^{2} }}{{n_{i} }}}} \right)} } \right]^{1/2} \)

    where σim and σc are be estimated by the sample standard deviations of \( y_{\text{it}}^{\text{im}} \) and \( y_{\text{ijt}}^{\text{c}} \).

    Note that an increase in the number of controls matched to each ith imprisoned individual (n i) disproportionally reduces the size of the standard error of the estimate of the treatment effect. This is the reason why we match up to three controls instead matching up to a single control.

  10. Overall, the justice systems in the US and Netherlands are in many ways similar—both have the same court personnel consisting of judges, prosecutors and defense counsel, both countries provide similar due process rights, and both utilize prison as the most serious sentencing option for offenders. However, a number of key differences also define the two justice systems. Plea bargaining dominates the American system but does not exist in the Netherlands, and juries are a key component of trials in the US but they are not used in the Netherlands. Instead the Dutch system relies on a panel of three judges to determine guilt and sentence. While the American system is more adversarial, relying on cross-examination of witnesses, Dutch judges rely heavily on information in case files.

  11. To allow for non linear relationship between age and imprisonment risk we also included age and age-squared as explanatory variables in the propensity score model.

  12. The cohorts are similar to those distinguished in Blokland et al. (2005) and Blokland and Nieuwbeerta (2005).

  13. The measure of offense severity ranges from 0 to 20. To improve the interpretation of the coefficients for the effects of type of offense dummies we centered the offense severity around the means of the corresponding offense dummies. For Opium and Gun Law offenses no offense severity measure was available.

  14. The final category in Monahan’s taxonomy measures what has been done to the individual. For this category we have no measurements but here we note that our extensive data on prior record is at least in part controlling for the enduring effects of early life experiences.

  15. In estimating the propensity scores only main effects of covariates were estimated—and no interaction terms (see Table 1).

  16. Some readers might question the use of individuals who are imprisoned after t as matched controls for individuals imprisoned at t. For such readers it is important to keep in mind several points. First, if we were reporting the results of a randomized experiment in which controls were sentenced to a non-custodial sanction, some of these individuals might subsequently be incarcerated for another offense. If they were excluded from the analysis the bias protection from randomization would be vitiated. Similarly if we were to exclude the later imprisoned as potential matches, this would have in fact been a source of bias. Second, it is important to keep in mind that treatments are administered at specific points in time and that treatment at time t does not in general preclude treatment or not at a later date. Consequently, treatment effects should be understood to be possibly time dependent. For a fuller discussion of these issues see Li et al. 2001).

  17. The formula for the standardized difference statistic—in percentages—as suggested by Rosenbaum and Rubin (1985:36) is:

    \( D = \left( {{\frac{{\bar{X}_{\text{w}} - \bar{X}_{\text{n}} }}{{\sqrt {{\frac{{s_{\text{w}}^{2} + s_{\text{n}}^{2} }}{2}}} }}}} \right) \times 100 \)

  18. One reviewer suggested that the practice of setting aside individuals with no suitable matches created rather than prevented bias. We strongly disagree. The individuals for whom we were unable to identify suitable matches all had very high probabilities of imprisonment. This was because they had very long criminal records and/or had been convicted of very serious crimes. These are precisely the types of variables which if left unaccounted for may seriously bias treatment effect estimates. Thus, to have included them in the analysis despite the fact that we had no suitable matches increases rather than decreases the risk of bias.

  19. We also note that the US itself is very large and diverse country. For this reason it is not self evident that findings based on a Hispanic population from the Southwestern US are any more generalizable to rural New England than are results from the Netherlands.

  20. Note that having been incarcerated may make it more likely that, ceteris paribus, an individual will subsequently be convicted of a later crime, as a result of a labeling process by judges. That is, if the take prior prison time as indicators of bad character, they might suffice with less tangible evidence to reach a guilty verdict.

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Acknowledgments

We thank Paul Rosenbaum for many valuable suggestions. All errors, however, remain our own. This work was funded in part by the National Science Foundation (NSF) (SES-99113700; SES-0647576) and the National Institute of Mental Health (RO1 MH65611-01A2).

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Authors and Affiliations

  1. Nederlands Studiecentrum Criminaliteit en Rechtshandhaving (NSCR)—Netherlands Institute for the Study of Crime and Law Enforcement, Leiden, The Netherlands

    Paul Nieuwbeerta & Arjan A. J. Blokland

  2. Utrecht University, Utrecht, The Netherlands

    Paul Nieuwbeerta

  3. H. John Heinz III School of Public Policy and Management, Carnegie Mellon University, Pittsburgh, PA, USA

    Daniel S. Nagin

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  1. Paul Nieuwbeerta
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  2. Daniel S. Nagin
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  3. Arjan A. J. Blokland
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Correspondence to Paul Nieuwbeerta.

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Nieuwbeerta, P., Nagin, D.S. & Blokland, A.A.J. Assessing the Impact of First-Time Imprisonment on Offenders’ Subsequent Criminal Career Development: A Matched Samples Comparison. J Quant Criminol 25, 227–257 (2009). https://doi.org/10.1007/s10940-009-9069-7

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