Estimating the incapacitation effect among first-time incarcerated offenders

Abstract

Objectives: To estimate how many offenses are averted through the incapacitation of first-time incarcerated offenders with sentences of two years or less. Methods: The counterfactual challenge of estimating criminal acts that would have been committed had the offender not been incarcerated is approached utilizing a matching design. Data comprise all offenders convicted in Sweden in 2018, matched on a vector of time-stable and time-varying covariates drawn from an extensive set of Swedish registers. Each incarcerated offender is matched to a nonincarcerated offender whose offending frequency is used to infer the incapacitation effect. Full sample estimates are provided as well as subgroup estimates for males, females, and various risk groups. Results: The annual incapacitation effect for first-time incarcerated offenders is estimated to be 0.53 when measured as the number of averted convictions and 1.14 when measured as the number of averted offenses that would have resulted in a conviction. For males, the annual number of convictions averted through incapacitation is 0.51, and for females 0.37. For the highest risk group, the annual number of averted convictions is 1.22, and the number of averted offenses resulting in conviction is 2.55. For offenders in the low-to-medium risk groups, the corresponding figures are approximately 0.31 averted convictions and approximately 0.68 averted offenses. Conclusion: For first-time incarcerated offenders, the incapacitation effect is modest and the heterogeneous effects found across different risk groups warrant considering whether the crime-preventive effect is sufficiently large for low-risk inmates and whether noncustodial sanctions might constitute an alternative that would ease overcrowding without producing any considerable risk for costs in terms of recidivism.

Introduction

In theory, the capacity of prisons to control crime is caused by their deterrent effect, which comes in the form of general or specific deterrence (Nagin, 1978). Their crime-reducing effect, however, also comes from physically incapacitating offenders (Zimring and Hawkins, 1995). Knowledge of the specific deterrent effects of prisons is increasing, and has according to some reached a level that makes it safe to say that the failure of custodial sanctions to reduce postrelease recidivism is now a “criminological fact” (Petrich et al., 2021). In a similar vein, recent studies that have specifically examined the association between incarceration length and recidivism have in general found a null effect (Al Weswasi et al., 2022; Berger and Scheidegger, 2021). Since numerous studies have now dismissed the specific deterrent effect of imprisonment, an argument could nonetheless be made that although incarceration may not deter crime, it may at least avert crime through incapacitation. This gives rise to the question of how large this crime-control effect might be, and whether it is sufficiently large to merit the increased use of incarceration.

While the overall imprisonment rate in both Europe (Aebi et al., 2022) and the United States (Carson, 2022) has fallen steadily since the early 2010s, the trend in Sweden has been the reverse. From the 1990s, the use of incarceration in Sweden declined until the mid-2010s but has since increased both in terms of average sentence length and the number of offenders sentenced to prison (Kriminalvården, 2021). In recent times, and in part due to a recent increase in gang-related violence, what was previously a partisan issue, with right-leaning parties pushing for tough-on-crime policies, has become a bipartisan issue, with parties on both sides of the political divide arguing for harsher sentences (Tham, 2022). As a result of the increasing prison population, the occupancy rate in Swedish prisons was 109% in 2021, and many inmates now have to share cells designed for single occupancy (Kriminalvården, 2021). Overcrowding has led the Swedish Prison and Probation Service (Kriminalvården) to state that they are now unable to ensure that they can operate “in a safe, humane and efficient manner” (Kriminalvården, 2019). As a consequence, violence or threats against staff and between inmates have increased over recent years. The long-term consequences of the policy shift toward harsher sentencing can also be observed in the annual forecasts made by the Swedish prison and probation service regarding future inmate numbers. In 2017, the number of inmates was 4148 and the current prediction for 2030 is that this number will have increased to 7430 (Kriminalvården, 2022). ¹ A substantial part of this increase is due to the increased use of incarceration for young adults in combination with tougher rules on early parole release. This increased use of incarceration directs a spotlight on the use of imprisonment as a means of controlling crime and on the issue of the size of such a crime-control effect. While the specific deterrent effect of incarceration is increasingly well understood, the magnitude of possible incapacitation effects is not as well-known as a result of methodological and contextual considerations.

The present study aims therefore to address the question of how many offenses are averted through the incapacitation of first-time incarcerated offenders with sentences of two years or less. In addition to aggregate estimates of the number of offenses averted via incapacitation, the study also explores effects by sex and risk group in order to provide greater insight into effect heterogeneity. The benefits of focusing on offenders who have been incarcerated for the first time are two-fold. Firstly, concentrating on offenders with no previous experience of incarceration prevents any effects of individual deterrence from previous imprisonment. Secondly, inmates who are incarcerated for the first time, on average, have a lower risk for recidivism than recidivists with prior experience of incarceration (Kriminalvården, 2021). This heterogeneity highlights the need to analytically differentiate between inmates to better understand different groups of inmates and their recidivism patterns.

Methodologically, studying incapacitation effects is a challenging task because what we are basically asking is how many offenses an incarcerated offender would have committed if the individual had not been incarcerated. Examining a hypothetical outcome of this kind requires counterfactual reasoning and some type of comparison group that has not been incarcerated and whose behavior can be used to infer the incapacitation effect. The challenge when comparing offenders sentenced to incarceration with offenders who have received a noncustodial sanction is that these two groups differ systematically in characteristics that affect both the probability of being sentenced to prison and the risk for recidivism (Bales William and Piquero, 2012a). The present study addresses this challenge by adopting a matching design that attempts to identify a suitable, nonincarcerated match for each incarcerated offender. In an effort to balance confounding factors, the nonincarcerated offenders are selected on a wide set of time-stable and time-varying observables and then matched on the likelihood of being incarcerated. Numerous factors can affect whether or not someone is imprisoned as a result of their offending. The seriousness of the offense, the offender's criminal history, and the judge's discretion are a few examples (Loeffler and Nagin, 2022). In addition, a person's race, sex, and labor market attachments may all have an impact on whether or not they are sentenced to incarceration (Bales William, 2012b; Doerner and Demuth, 2014). The observables in this study cover full criminal history, hospitalization for drug or alcohol abuse or mental health issues, family criminal and mental health history, school performance, labor market attachment, living conditions, and other personal characteristics. After matching, the nonincarcerated sample is then observed for a period of time, and their offending frequency during this period is used to estimate the incapacitation effect.

Literature review: Approaches and challenges when estimating incapacitation effects

In the criminological literature, incapacitation effects have traditionally been expressed in terms of the number of offenses averted by incarcerating an offender for one year. The fundamental problem associated with estimating incapacitation effects is of a counterfactual nature; we are limited to estimating the value of the offending frequency while incarcerated without any knowledge of how this frequency would have unfolded if the offender had not been incarcerated. One of the first pieces of research that attempted to estimate incapacitation effects and to overcome this counterfactual challenge was the RAND Corporation's inmate studies, which surveyed incarcerated offenders in the 1970s with regard to, among other things, their offense frequencies during the year leading up to their prison sentence. Borrowing terminology from criminal careers research, this estimate of the annual offending frequency has often been referred to as λ: the Greek letter lambda (Blumstein, 1986). Applying this within-individual approach to microlevel data, the RAND Corporation inmate studies estimated that lambda was between 187 and 287 offenses and that this was thus the annual incapacitation effect (Chaiken et al., 1982; Peterson and Braiker, 1980). Generalizing lambda from behavior prior to a prison sentence—and using an in essence within-individual design—has, however, been criticized for producing a considerable overestimation (Blumstein, 1986; Spelman, 2000). In part, this overestimation follows from some respondents answering that they have committed exceptionally many crimes but also from so-called crime spurts, that is, unusually high crime frequencies shortly before an offender's prison sentence, which limit the usefulness of inferences drawn on the basis of such a window period (Zimring and Hawkins, 1995).

Another early approach to estimating incapacitation effects was the use of macrolevel data consisting of aggregated crime rates in combination with prison population data (mainly from the United States) with the aim often being to establish the percentage change in the crime rate (i.e., the elasticity of the crime rate) associated with a certain percentage change in the incarceration rate (Piquero and Blumstein, 2007). As noted in a systematic review by Stemen (2007), estimates from these early studies of the effect of a 1% increase in the incarceration rate ranged from no change to a 2.8% decrease in crime rates. The problem with early macrolevel studies was that they failed to account for the simultaneity of crime rates and the prison population (Durlauf and Nagin, 2010). An increase in crime rates may increase the prison population, but it could also be the case that an increase in the prison population increases the crime rate, and in order to obtain valid elasticity measures the causal order must be identified. Macrolevel studies have also been criticized for being incapable of separating incapacitation from deterrence effects (Spelman, 2000).

Later studies have attempted to overcome the limitations of earlier research by utilizing natural experiments. One of the first studies to adopt a quasi-experimental design was by Owen (2009), who utilized a change in Maryland's sentencing guidelines that resulted in an overall reduction in the length of incarceration for young adults aged 23–25. The sentence reduction resulted in an average increase of 2.8 arrests per year per person (of which 1.6 were for drug offenses) and an average increase of 2.9 index offenses per year per person. Buonanno and Raphael (2013) utilized the quasi-experimental nature of the 2006 Italian collective pardon that affected one-third of the nation's prison inmates. The authors found that between 14 and 46 reported offenses were averted per person per year and that most of these offenses were thefts of various kinds. Barbarino and Mastrobuoni (2014) also utilized the variation in the prison population created by Italian collective pardons. After assessing eight different pardons awarded between 1962 and 1990, the authors found that a 1% decrease in the prison population resulted in a 17–30% increase in crime. Tollenaar et al. (2014) analyzed a 2004 Dutch policy reform that increased prison sentences considerably for repeat offenders—even if the offenses committed were relatively minor. Utilizing propensity score matching, the authors matched habitual offenders who were affected by the reform to a control group of nonaffected habitual offenders who had on average shorter sentences. In order to estimate the size of the incapacitation effect, the convictions and the recorded offenses in the control group were counted in the remaining period the habitual offenders who were affected by the reform were incarcerated. The estimated annual incapacitation effects were estimated at 2.5 convictions and four recorded offenses, of which a majority of the recorded offenses were related to theft and shoplifting in particular. Observing the period after release and utilizing recidivism during this period as the counterfactual incapacitation effect has its limitations since it is difficult to separate between the counterfactual incapacitation effect and the deterrent or criminogenic effects from the recently served prison sentence.

An alternative approach to specifying incapacitation effects without the interference of other processes, such as the one described above, is to utilize a matching design to match incarcerated to nonincarcerated offenders. The matched nonincarcerated sample is then used as the counterfactual and the mean annual number of registered offenses committed by these individuals represents the incapacitation effect. Only two studies have to date used this approach and both have observed first-time incarcerated offenders. The first to use the approach were Sweeten and Apel (2007) who employed data from the National Longitudinal Survey of Youth 1997 (NLSY97) to construct a wide set of time-stable and time-varying covariates focused on criminal history, demographics, academic achievement, and social and economic characteristics in a study population of young offenders aged 16 to 19. These covariates were then used to construct a propensity score for being incarcerated, which was in turn utilized to match incarcerated offenders to nonincarcerated offenders. The study then estimated that for offenders aged 16–17, one year of incarceration prevented between 6.2 and 14.1 offenses, while for offenders aged 18–19 a year of incarceration prevented between 4.9 and 8.4 offenses. Because the authors utilized survey data on individuals’ self-report participation and frequency of offending, under-reporting was less of an issue than it is for studies that use offenses reported to authorities as the measure of crime. However, the authors reported that NLSY97 has a nontrivial attrition rate, which might result in an underestimation of the incapacitation effect.

The second study to use a matching design to examine this issue was conducted by Wermink et al. (2013). Their data comprised the official criminal records of all individuals convicted in the Netherlands in 1997. The study employed a narrower set of covariates than that used by Sweeten and Apel (2007), focusing on the offenders’ sex, age, birthplace, and criminal history. The authors found that the overall annual incapacitation effect amounted to 0.21 averted convictions. When stratified by age and sex, the authors found the annual incapacitation effect to be 0.22 convictions for males, 0.12 convictions for females, 0.32 convictions for juveniles, and 0.2 convictions for adults. Using information on the ratio between the number of annual convictions and the number of crimes reported to the police, the authors estimated that for those serving their first term of imprisonment, between 2.04 and 2.52 registered offenses were avoided per year of incarceration.

Current study

Based on the above literature review, the present study aims to extend the previous research concerning incapacitation effects by specifically addressing some of the limitations that have affected the research to date. Firstly, this study includes data that are more recent than those employed in previous studies. Much of the existing literature has utilized data from the 1990s or early 2000s. This is a limitation that is worth addressing given the overall decline in crime rates witnessed both in Sweden (Bäckman et al., 2020) and other parts of the world (Tseloni et al., 2010), since this decline may also impact the size of the incapacitation effect. Similarly, the use of more recent data also makes the findings more policy-relevant. The second limitation addressed by the study is that comparing recidivism rates between countries—even within Europe—is known to be challenging as a result of differences in criminal justice systems and composition effects (Aebi, 2010) which is why measuring the incapacitation effects in various contexts is necessary. In addition to methodological reasons, the observed differences in incapacitation effects found in the studies described in the literature review could be derived from the fact that the studies in question are done in different contexts with various characteristics in the prison population. The incapacitation effect in, for example, a prison population with large numbers of offenders incarcerated for drug and property crimes may potentially be larger than in a prison population dominated by offenders with crime types associated with smaller recidivism risks. The third limitation that this study attempts to address relates to the use of the matching design. The ability to properly match incarcerated to nonincarcerated offenders is in large part dependent on the covariates employed. Nagin et al. (2009) have argued that as a bare minimum, the covariates employed should include sex, age, race, and criminal history. There are few good arguments for not including more covariates, however, since additional covariates increase the balance between the treated and nontreated groups. The current study utilizes several high-quality Swedish registers, which provide a rich and extensive set of covariates that are known to predict both the treatment and outcome that constitute the focus of this study, but that could also potentially control for crucial unobservables (Loeffler and Nagin, 2022). Finally, the issue of heterogeneity in the incapacitation effect has not been fully explored and is therefore something that we know relatively little about. In addition to presenting aggregated estimates and estimates by sex, this study therefore also directs special attention to the incapacitation effect for various risk groups who have varying propensity scores in relation to being sentenced to prison.

Data and operationalization

Treatment status: Incarceration and nonincarceration

In order to estimate the incapacitation effect for first-time incarcerated offenders, data were gathered on all offenders with a personal identification number who were convicted in Sweden in 2018 (N = 72,009). ² Convictions are drawn from the Convictions Register maintained by the Swedish National Council for Crime Prevention (BRÅ) and cover the period 1973 to 2020. Since the age of criminal responsibility is 15 in Sweden, having access to these data means that the entire conviction histories of all cohorts born after 1957 were accessible. Individuals below the age of 18 are rarely sentenced to prison in Sweden, and the study has therefore excluded convictions for individuals who were under the age of 18 when the crime resulting in the conviction had been committed (N = 8206). Since having access to records of previous criminal activity is essential for predicting both the likelihood of being sentenced to incarceration and postrelease recidivism, all convictions for individuals born prior to 1958 have been removed (N = 5106). The age range for the offenders included in the study is therefore 18–60. Since the study focuses on offenders sentenced to prison for the first time, all convictions for offenders who had been incarcerated prior to 2018 have been excluded (N = 13,339). ³ Offenders who had been sentenced to youth care (N = 37), psychiatric care or care in accordance with the Care of Abusers (Special Provisions) Act (N = 167) were also excluded, since these sentences may also incapacitate offenders wholly or in part. Individuals who had received a combination of probation and incarceration (N = 137) or a sentence that ended in no sanction (often used for mentally disturbed offenders) have also been excluded (N = 11). Relatively few offenders in Sweden are sentenced to terms of more than two years imprisonment, and these have therefore been excluded (N = 565). They were also excluded because individuals who are sentenced for serious offenses (which often result in sentences of more than two years) may have additional unobservables and are thus less comparable to the nonincarcerated sample. Offenders who died during the period 2018–2019 (N = 476) have also been excluded from the study. ⁴

Following these restrictions, the final number of convicted individuals included in the study was 43,940 (61% of the original sample). For the index conviction (i.e., the first conviction each offender received in 2018 that qualified them for inclusion in the study), 29,537 offenders received a fine, 8135 received a conditional sentence, 2937 received a prison sentence, ⁵ 2097 were sentenced to probation, and eight were sentenced to youth service. The individuals in the incarcerated sample (N = 2937) constitute the treated sample, and the offenders who received a sanction other than incarceration (N = 41,003) comprise the nontreated sample. The types of punishments in the nontreated sample are qualitatively different both in terms of what the punishments entail and also the characteristics of those who in general receive the penalty in question. Not restricting the types of punishment in the nontreated sample has the benefit of ensuring a comprehensive sample and letting the matching procedure identify those individuals that have the most resemblance to the treated sample from an otherwise heterogeneous group.

Covariates and data sources

All residents in Sweden have a personal identification number that is used by the Swedish authorities for administrative purposes. This identification number makes it possible to link various administrative data sources. ⁶ In order to create a better balance between the treated and nontreated samples, five broad categories of covariates were created using data from multiple linked registers. Each category includes both time-variant and time-invariant covariates. The first category focuses on criminal history and is based on data drawn from the Convictions Register and the Register of Suspected Offenders. One of the strongest predictors of recidivism is the level of prior involvement in crime, and for all offenders in the study a range of information on their criminal histories, such as the number and type of registered offenses, has been extracted for all their convictions prior to the index conviction in 2018. Being sentenced to incarceration is more likely if an offender has previously committed an offense of a similar type and a dummy variable has therefore been created indicating whether the offender had committed a similar offense during the five previous years. Data were also extracted from the Convictions Register on sibling and parental criminal histories, which indicate whether any sibling or parent had been either convicted or incarcerated after 1972. ⁷

The second category of covariates has been drawn from the Longitudinal Integrated Database for Health Insurance and Labor Market Studies, maintained by Statistics Sweden, and includes information on labor market attachment, more specifically, income and social welfare recipiency during the years leading up to the index crime. Labor market attachment is a particularly important covariate since it can affect whether or not an offender is given a prison sentence. The School Register is also maintained by Statistics Sweden and has been used for the third category of covariates, which focus on school performance in lower secondary and upper secondary schools. The fourth set of covariates is based on data from the National Patient Register—maintained by the National Board of Health and Welfare (Socialstyrelsen)—and these focus on the offender's, parental and sibling inpatient and outpatient care for drug and alcohol-related issues or mental health issues during the five years leading up to the index conviction. A measure was also obtained from the same register on whether an offender had received hospital care for violent victimization. Finally, a range of demographic covariates were generated focused on offender-specific and family characteristics, such as family composition and country of birth. ⁸ Since the presence of children may impact judges’ decisions on whether or not an offender should receive a prison sentence, a dummy variable was created indicating whether an offender had a child. Descriptive statistics on all the included covariates are presented in Table A.2 in the Appendix for both the incarcerated and nonincarcerated samples.

Outcome measure

Before moving on to describe the crime measures employed in the study, this section first describes the two time-at-risk periods employed for the estimation of the incapacitation effect. First, the number of averted offenses is expressed in terms of an annual frequency, which is in line with the way incapacitation effects (i.e., lambda) have traditionally been presented in the literature. The time-at-risk starts on the day following a conviction and the nonincarcerated offender is then observed for 365 days. Offenses committed during this period are then used to infer the incapacitation effect. A second operationalization of time-at-risk adjusts this period to make it more context-specific to Sweden and observes the nonincarcerated offender for the period of the matched counterpart's prison term. For example, if a nonincarcerated offender has been matched with an incarcerated offender serving a three-month prison term, then the nonincarcerated offender is observed for three months, starting from the day following the nonincarcerated offender's conviction date. Figure 1 presents the distribution of the length of incarceration among the selected incarcerated offenders.

Figure 1.

Prison sentence length distribution.

The current study measures offenses averted as a result of incapacitation in two ways. The first measure counts the number of reconvictions following the index conviction during each of the two time-at-risk periods described above. The second measure has been produced by extracting information on the offenses included in each of these subsequent convictions, and the dates on which they were committed, and constitutes a measure of convicted offending frequency that describes the number of offenses resulting in the conviction that were committed during each of the two time-at-risk periods. As opposed to the measure based purely on the reconviction date, the offense frequency measure utilizes the dates of the offenses committed during the periods-at-risk. ⁹ Hence, convictions after time-at-risk are included in the averted convicted offending frequency as long as the convicted offenses are committed during time-at-risk.

The estimated incapacitation effect is obtained using the following equation:

$$\mathit{I}\mathit{n}\mathit{c}\mathit{a}\mathit{p}\mathit{a}\mathit{c}\mathit{i}\mathit{t}\mathit{a}\mathit{t}\mathit{i}\mathit{o}\mathit{n}\mathit{e}\mathit{f}\mathit{f}\mathit{e}\mathit{c}\mathit{t}={\displaystyle \frac{{\sum }_{\mathit{i}=1}^{\mathit{n}}{\mathit{x}}_{\mathit{i}}{\mathit{w}}_{\mathit{i}}|\mathit{T}=0}{{\sum }_{\mathit{i}=1}^{\mathit{n}}{\mathit{w}}_{\mathit{i}}|\mathit{T}=0}}$$

(1)

where x is the number of convictions or offenses resulting in a conviction for the ith nontreated (i.e., nonincarcerated) offender, multiplied by the weight w for the ith nontreated offender divided by the total sample weight w in the nontreated sample. The weight is calculated as the number of times ith offender is matched to a treated (i.e., incarcerated) offender. Confidence intervals for the mean values are generated from the 5th and 95th percentiles of 10,000 bootstrap estimates based on the matched nonincarcerated sample. As a result of the presence of extreme outliers that have a substantial effect on the mean number of offenses, the variable indicating the number of offenses for which an offender has been convicted was winsorized at the 97.5th percentile.

Method: A matched samples approach

The present study has been guided by the work of Sweeten and Apel (2007) and Wermink et al. (2013) who estimated incapacitation effects utilizing propensity score matching to match incarcerated offenders to nonincarcerated offenders. Within the field of criminology, matching designs have been widely used not only to estimate incapacitation effects but also to compare the effects of custodial and noncustodial sanctions on various outcomes (for an overview of studies utilizing the matching design, see for instance Apel and Sweeten, 2010; Villettaz, Gillieron and Killias, 2015).

Matching procedure

When conducting propensity score matching, the first step is to estimate the conditional probability of being assigned the treatment. In this study, this has been achieved by means of a logit model that predicts the probability of being sentenced to prison in 2018—conditional on the observed covariates. Since the logit model is only used to provide the predicted probability for each observation, issues concerning collinearity or overfitting are not a problem. The outcome of the logistic regression is presented in Supplemental Table S1. It shows that the covariate that has the strongest association with the dependent variable—and thus also with the propensity score—is if the principal offense in the index conviction is a sex crime (odds ratio = 3.5, p < .001), followed by if the offender has been convicted for fraud within five years prior to index conviction (odds ratio = 1.51, p = .003), and being hospitalized for drug abuse within five years prior to index conviction (odds ratio = 1.49, p = .03).

Each treated offender is then matched to a nontreated offender with replacement, and with a narrow caliper set to 0.1, which means that within each pair, the maximum distance for the predicted propensity score is 0.1 standard deviations. A narrow caliper setting minimizes the within-pair difference in propensity scores and therefore, given the vector of covariates, increases the likelihood that the nonincarcerated sample will mirror the incarcerated sample. As a robustness check, estimated incapacitation effects after matching with various caliper widths will be presented in the results section. There are a range of possible matching methods and algorithms, and nearest neighbor matching with replacement within specified caliper width, which is the method used in this study, is often recommended (Austin, 2014), especially if the nontreated sample is much larger than the treated sample. Generally speaking, matching designs are best suited to large sample sizes and a sample size above 1500 is generally viewed as a reasonable basis for a well-designed matching study (Shadish, 2013). Consequently, having more than 41,000 individuals in the nontreated sample increases the robustness of the current study. One drawback with nearest-neighbor matching is that it may result in a large number of unmatched nonincarcerated. Therefore, generalized full matching, which is a variant of full matching, is also presented as a robustness check (Sävje et al., 2021). This matching algorithm has the advantage of utilizing all the individuals, by assigning every incarcerated and nonincarcerated unit in the sample to one subclass each and then providing a weight to each individual which is then used to estimate the incapacitation effect.

Matching on propensity scores has been criticized for reducing multivariate dimensionality to a single matching score, which could result in matches that have similar propensity scores but are nonetheless far from similar on many covariates (King and Nielsen, 2019). Various matching algorithms were tested, and nearest neighbor was chosen as it yielded the best overall balance without producing too many unmatched units. Matching was conducted using the R package MatchIt Version 4.5.4 (Ho et al., 2011).

The overall covariate balance between the treated and the nontreated groups is primarily assessed via the standardized mean differences (SMD) measure first described by Rosenbaum and Rubin (1985). The SMD is given by the following equation:

$$\mathit{S}\mathit{M}\mathit{D}={\displaystyle \frac{{\overline{\mathit{x}}}_{\mathit{t}}-{\overline{\mathit{x}}}_{\mathit{c}}}{\sqrt{\left({\displaystyle \frac{{\mathit{s}}_{\mathit{t}}^2+{\mathit{s}}_{\mathit{c}}^2}{2}}\right)}}}$$

(2)

where ${\overline{x}}_t-{\overline{x}}_c$ is the difference in the mean of each individual covariate between the treated and nontreated groups, standardized by a standardization factor which in this study is the pooled standard deviation across both groups. In order to observe the extent to which balance is improved, the SMD is measured both prior to and after matching. There is no consensus regarding the maximum SMD value for an acceptable level of covariate balance but a threshold of 0.1 is recommended (Austin, 2011), and this threshold has been used in the present study. Although balance is not in itself an indicator of strong ignorability, having a good balance is necessary to satisfy the strong ignorability assumption (Shadish, 2013).

Because the present study will also include subgroup analyses, matching was also conducted separately by gender. There are different strategies for conducting propensity score matching for subgroup analysis and one recommended approach involves using propensity score estimation and matching separately within subgroups (Green and Stuart, 2014; Wang et al., 2017, 2018). One advantage of subgroup-specific matching is that it makes balance diagnostics more accessible, thus enabling the researcher to ensure that balance is achieved—even within each subgroup. A consequence of breaking down the sample by sex is that the sample sizes become smaller, which in turn results in greater difficulties in achieving a good balance.

Results

Matching results and balancing diagnostics

As can be seen from Table 1, a suitable nonincarcerated match was identified for all of the 2937 incarcerated offenders. Among the 2564 matched nonincarcerated offenders, 63% received a fine, 23% received a conditional sentence, and 14% were sentenced to probation. The unmatched nonincarcerated offenders are predominantly found on the lower end, with only a small portion having propensity scores larger than 0.1 (see Figure A.1). As will be shown in the risk group heterogeneity analysis, offenders with the lowest propensity score also have on average the lowest incapacitation effect. ¹⁰ To better understand how the unmatched individuals in the nonincarcerated sample may impact the incapacitation effect, a full matching algorithm is used as a robustness check and discussed further below.

Table 1.

Sample sizes before and after matching.

	Nonincarcerated	Incarcerated
Group
All	41,003	2937
Matched	2564	2937
Unmatched	38,439	0

Notes: Table shows the number of matched and unmatched individuals in the nonincarcerated and incarcerated sample after matching. Since matching is done with replacement, the number in the matched nonincarcerated sample reflects unique individuals with some being matched multiple times

Figure 2(a) presents the distribution of the predicted propensity for being sentenced to prison among all those who were sentenced to prison and all those who received a sanction other than imprisonment, prior to matching. As can be seen, there is an overlap in the range of propensity scores across the incarcerated and nonincarcerated groups, which means that there is common support in terms of matchable offenders in both groups and across propensity scores (Caliendo and Kopeinig, 2008). The predicted incarceration propensity is greater among those who received a prison sentence than among those who did not. This shows that the offenders who received a prison sentence are on average different from the individuals who were given a noncustodial sentence, and we would therefore be at risk of violating the strongly ignorable treatment assignment assumption which states that conditioned on the vector of covariates, the potential outcome must be independent of the treatment (Lechner, 2001). Figure 2(b) shows the same propensity distribution subsequent to matching, and the near-mirror image of the distributions provides a first indication that the matching procedure has been successful.

Figure 2.

Propensity distribution prior to and after matching among the nonincarcerated and incarcerated.

Figure 3 presents the absolute SMDs for each of the covariates in the sample prior to and after matching. For example, the gray dot at the upper-right extreme of the diagram represents the SMD value for the number of offenses for which an offender has been suspected prior to the index conviction, which is the covariate with the highest SMD (0.41) prior to matching; after matching, the absolute SMD for this covariate is 0.01 (the top black dot on the left of the diagram). Since few covariates display acceptable SMDs in the original sample, matching was necessary to achieve balance. As can be seen from Figure 3, all black dots—indicating the absolute SMD after matching—are to the left of the vertical line that indicates an absolute SMD of 0.1. Only two of 100 covariates in total have an absolute SMD value above 0.05 (none were above 0.1) implying that the matching procedure was very successful in achieving a balance between the matched incarcerated and nonincarcerated groups.

Figure 3.

Absolute standardized mean differences for each covariate prior to and after matching.

The above balance diagnostics are also presented in Table A.1 of the Appendix. The imbalance is greatest for the criminal history covariates and for these, the mean values are with few exceptions higher for the incarcerated than for the nonincarcerated sample. For example, the average number of prior offenses resulting in the individual being registered as a suspect is 10.5 for the incarcerated sample and 4.8 for the nonincarcerated sample, which can be translated into an SMD of 0.41, which is well above the acceptable threshold. The mean number of previous convictions is 4.26 in the incarcerated sample and 2.73 in the nonincarcerated sample, which represents an SMD of 0.39.

As can be seen from Table A.2(a) in the Appendix, 99.7% of the incarcerated male offenders were successfully matched. For females, a match was found for 96.1% of the inmates (Table A.2(b) in the Appendix). Appendix Figure A.3 shows that the unmatched offenders among both males and females are in large part offenders found in the higher end of the propensity distribution. Figure A.2(a) in the Appendix shows the covariate balance for males, while Figure A.2(b) shows the balance for females. None of the absolute SMDs for males are above 0.1 indicating that matching was successful. Since the female sample was relatively small, there were some difficulties in achieving balance. Five covariates had absolute SMD values of between 0.1 and 0.12, and the covariate indicating if the offender was born in Sweden but with parents from a Western country other than Sweden had an absolute SMD of 0.17. Although the balance for these three covariates is close to the acceptable threshold, the lack of complete balance and the number of unmatched female inmates may place limitations on interpretations of the incapacitation effect for females.

Incapacitation effect among first-time incarcerated offenders

This section first describes the estimated incapacitation effect measured as averted convictions and then in terms of averted offenses resulting in a conviction. Averted convictions and offenses are both described per incarceration year and per the average Swedish prison sentence, and separate estimates are presented for females, males, and the full sample. The distribution of different categories of offenses within the averted offense estimate is then presented, before finally presenting the estimated incapacitation effects for various risk groups.

Starting with Table 2(a), we see that the estimated incapacitation effect for the full sample is 0.53 averted convictions per prison year. This means that an average of 0.53 convictions are avoided when an offender who has never previously served a prison term is sentenced to one year in prison. The annual incapacitation effect is 0.51 convictions for males and 0.37 convictions for females. When the time-at-risk is set to the length of an average Swedish sentence, the number of averted convictions shrinks to 0.33 for the full sample. The number of averted convictions per average incarceration length is 0.35 for males and 0.19 for females. Moving on to Table 2(b) and the averted offenses resulting in a conviction, we see that incarcerating an offender for one year on average prevents 1.14 such offenses or 0.73 per average prison sentence. ¹¹ We see a tendency for the number of averted offenses to be larger for males than for females irrespective of the time-at-risk.

Table 2.

Estimates of the number of convictions and offenses resulting in a conviction that is averted due to incapacitation. Ninety-five percent bootstrap confidence intervals in parenthesis.

	(a) Convictions averteddue to incapacitation		(b) Offenses that would have resulted in a conviction averted due to incapacitation
	Perincarceration year	Per average incarceration length	Perincarceration year	Per average incarceration length
Group
Female (n = 357)	0.37 (0.29–0.45)	0.19 (0.14–0.26)	0.78 (0.60–0.97)	0.37 (0.26–0.49)
Male (n = 2179)	0.51 (0.47–0.55)	0.35 (0.32–0.39)	1.17 (1.08–1.27)	0.74 (0.67–0.81)
Total (n = 2564)	0.53 (0.49–0.56)	0.33 (0.30–0.36)	1.14 (1.06–1.23)	0.73 (0.66–0.79)

Notes: Table shows the average number of convictions (Panel a) and the average number of convicted offenses (Panel b) in the matched nonincarcerated sample. Matching is done by nearest neighbor matching with replacement with caliper width of 0.1. Each nonincarcerated individual has information on sentence length, extracted from the matched incarcerated individual and is used to estimate the incapaciation effect by sentence length. The estimates by sex are from separate matching procedure for each sex.

Figure 4 breaks down the annual incapacitation effect of 1.14 offenses resulting in a conviction into offense categories and presents the proportion of the averted offenses accounted for by each offense category. The largest portion of the annual incapacitation effect is comprised of narcotics offenses (0.4 offenses annually) which account for 35% of the annual estimate of the offenses resulting in a conviction that is averted through incapacitation. These are followed by traffic offenses (0.36 offenses annually) which account for 31% of the estimate, and violent crime (0.21 offenses annually), which accounts for 19% of the estimate of averted offenses.

Figure 4.

Offense category proportions of the annual number of offenses averted through incapacitation.

Figure 5 presents the estimated number of convictions and offenses resulting in a conviction that is averted through incapacitation in relation to 10 quantiles of the offender sample specified on the basis of their propensity scores. These deciles range from offenders with the lowest predicted propensity for incarceration—given the vector of covariates—to the decile of offenders with the highest risk of incarceration. The dark gray bars represent the annual estimates, and the light gray bars represent the estimates for the average sentence length. For the number of convictions averted through incapacitation, similar incapacitation effects are found for deciles 1 through 4. For offenders in decile 4, the annual incapacitation effect is 0.31 averted convictions (Figure 5(a)) and 0.68 averted offenses (Figure 5(b)). The incapacitation effect then increases and for offenders in decile 10, for which the largest incapacitation effect is greatest, the incapacitation of an offender for one year prevents 1.22 convictions or 2.55 offenses that would have resulted in a conviction.

Figure 5.

Convictions and offenses averted through incapacitation by propensity score strata.

As a robustness check, the incapacitation effect was remeasured with various caliper widths. As discussed in the methods section, a narrower caliper decreases the distance in propensity score within each matched pair but with the risk of an increase in unmatched individuals. Furthermore, an additional matching algorithm was implemented in order to see if the estimated effect was sensitive to the chosen matching method. As seen in Appendix Table A.3, matching with the provided calipers produces a similar incapacitation effect as found in the main results. In terms of the generalized full matching algorithm, the estimated averted convictions were practically identical to the effect found in the main results. Averted offenses that led to a conviction were outside the confidence interval from the estimate in the main result but the difference in estimate was only 0.15 offenses.

Discussion

Incarceration may arguably have a crime-control capacity in terms of its incapacitation effect. The magnitude of this effect is not fully understood, however, given that the effect is variable depending on the context and changes in general crime frequencies over time. Also, the effect is difficult to estimate since it requires counterfactual reasoning regarding the behavior that an incarcerated offender would have engaged in had the individual not been sent to prison. From a wide set of time-variant and time-invariant vector of covariates, offenders sentenced to incarceration in Sweden in 2018 have been matched to “statistical twins” who were also convicted in 2018 but who received a sentence other than incarceration. The nonincarcerated offenders have then been observed for a period of time and their offending behavior during this period has been used as the counterfactual for the incarcerated offenders and thus the incapacitation effect.

The results show that for a first-time incarcerated offender, the annual incapacitation effect is 0.53 when measured in terms of averted convictions and 1.14 when measured in terms of the number of offenses that would have resulted in a conviction. Two-thirds of the estimated averted offenses comprise narcotics or traffic offenses. For males, the number of annual averted convictions due to incapacitation is 0.51 and the corresponding figure for females is 0.37. The number of offenses averted annually is 1.17 for males and 0.78 for females. The results also show that for a first-time incarcerated offender in the highest-risk group, 1.22 convictions are averted annually and 2.55 offenses that would have resulted in a conviction. For offenders in the medium-risk groups, the corresponding figures are 0.31 convictions and 0.68 offenses.

With these results in mind, it is necessary to stress that the estimated incapacitation effect does not describe the overall net effect of incarceration. Alongside general deterrence, the effect of a prison sanction comes with the intention to also impact inmates’ postrelease behavior. While some studies show that incarceration may reduce reoffending, others show that the use of incarceration—as opposed to a noncustodial sanction—may have a criminogenic effect on some offenders (Nagin et al., 2009; Petrich et al., 2021). Consequently, any crime-reducing effects from incapacitation might in the long run be canceled out if the focus is instead directed at net effects. This may be especially true for young adults, who are more receptive to the detrimental effects of incarceration (Koops-Geuze et al., 2023; Koops-Geuze and Weerman, 2023; Lipsey, 2009). Further, the effects of incarceration are also not only experienced by those who are incarcerated, since there is evidence for collateral damage in terms of, for example, criminogenic effects resulting from exposure to parental incarceration during childhood (Dobbie et al., 2018; Wildeman and Andersen, 2017).

Attempting to contrast the estimated incapacitation effects found in this study to those reported in others involves a number of challenges, since studies vary with respect to both sample composition and the way incapacitation effects are measured. The annual incapacitation effect found in this study is somewhat larger than that found by Wermink et al. (2013). The results reported both by Wermink et al. (2013) and in the present study show that the incapacitation effect is larger for males than females. Differences in the incapacitation effect may be due to composition effects since Sweden incarcerates drug offenders to a greater extent than the Netherlands. The study by Wermink et al. (2013) is nonetheless one of only a few comparable studies since both they and the current study have estimated incapacitation effects by observing adult, first-time incarcerated offenders and utilizing measures of recorded crime. Apel and Sweeten (2007), who also employed a matching approach and focused on first-time incarcerated offenders, found an incapacitation effect that was substantially higher than that noted in the current study. However, this may be attributed to the fact that Apel and Sweeten focused on young offenders aged 16–19 and their use of self-reported crime data.

Estimating incapacitation effects on the basis of convictions and offenses resulting in convictions may represent a considerable limitation, and the results from this study should therefore be viewed as lower-bound estimates. Although measures of self-reported crime suffer from attrition that could in turn bias estimates of the incapacitation effect downwards, it could still be argued that this bias is not as substantial as the bias that is produced by being limited to crime measures based on convictions. At the same time, however, both the RAND Corporation's inmate studies and other incapacitation studies that have utilized self-reported crime data have been criticized for overestimating the incapacitation effect (Blumstein, 1986; Spelman, 2000).

One way of approaching the actual number of offenses prevented is to multiply the estimated number of averted offenses that would have resulted in a conviction by the ratio of reported offenses to offenses resulting in a conviction. In 2018, 1,550,000 offenses were reported to the police in Sweden and 101,000 convictions were issued (BRÅ, 2019a, 2019b). This means that there is one conviction for every 15.3 reported offenses. Multiplying the estimated annual incapacitation effect in terms of averted convictions by 15.3 results in eight reported offenses having been averted through incapacitation (or 5.2 averted reported offenses if the estimate is made using the average sentence length as the time-at-risk). This estimate is in line with the incapacitation effect found by Sweeten and Apel (2007). Still, the issue remains that not all offenses are reported, and according to the Swedish Crime Survey, only one-third of all offenses against the person are reported to the police, and approximately half of property offenses (BRÅ, 2021).

Another possible limitation when estimating the incapacitation effect concerns the issue of replacement. One core assumption when estimating incapacitation effects is that the offenses averted through incapacitation should not be replaced by another offender's criminal acts (Miles and Ludwig, 2007; von Hofer, 1993). Up until now, the estimated incapacitation effect has been described as a lower-bound estimate, although the possibility of unobserved replacement means that the estimated effect might just as well be viewed as an overestimation. A crime category with a large potential for replacement is drug dealing and given that drug crimes accounted for the largest share of the incapacitation effect found in this study, concern for overestimation could arise. This should, however, not be an issue since the averted drug crimes in question are predominantly possession of narcotics for personal use and other minor drug offenses. A second potential cause of overestimation that affects many incapacitation studies—the present study included—is that incapacitation effects are often measured as the offenses averted due to the offender being incarcerated. The problem with this operationalization is that crimes are not limited to acts committed outside prison; crimes are also committed in the prison environment. Not accounting for this is a possible second source of upward bias.

Although a matching design has been used in a wide range of incarceration studies (Apel and Sweeten, 2010), the matched sample approach comes with potential limitations. In the present study, the covariate balance between incarcerated and nonincarcerated offenders was very good following matching. Still, there may be issues with omitted variable bias and a potential unbalance in unobservables, which could impact both the risk for incarceration and recidivism. In a literature review concerning the impact of incarceration on recidivism, Loeffler and Nagin (2022) argue that worries about omitted variable bias may sometimes be overestimated. This argument is based on the authors having noted that when using the same data, regression analyses that were limited to observed case characteristics in general produced similar estimates and significance levels as models that are perceived as being more robust, such as regression discontinuity or instrumental variable designs. This does not downplay the importance of a well-considered research design but shows instead that the use of a rich set of covariates could indirectly adjust for unobservables (Stuart, 2010). In the present study, what is potentially lacking is information regarding personality traits that are theoretically linked to both incarceration risk and reoffending. This risk of a potential imbalance in personality traits might result in a violation of the strong ignorability assumption. Although the field of labor economics is distinct from criminology, it is worth highlighting that when Caliendo et al. (2017) studied labor market policies, they found that the exclusion of personality traits did not affect their point estimates. This may indicate that the omission of variables that are usually unobserved does not necessarily indicate a threat to the validity of the estimated effects—as long as the included covariates are broad, rigorous, and well thought out. The strongest predictor of criminal recidivism is past offending, and the advantage of the data used in this study is that they include the complete criminal histories of all offenders. Furthermore, the potential provided by high-quality Swedish registers has been fully utilized in the present study by linking multiple registers in order to generate a rich vector of covariates that extends far beyond the number of covariates viewed as constituting a reasonable minimum for studies of this kind. Having access to data on offenders’ school performance, labor market attachments, living conditions, hospitalizations for drug and alcohol abuse or mental health issues, family criminal and mental health histories, and other personal characteristics substantially improves the predictive ability of the model employed and most importantly has the capacity to indirectly control for crucial unobservables.

It should also be stressed that the focal point of interest in this study has been the incapacitation effect but incarceration has from a societal and policy perspective a multitude of justifications. In addition to general deterrence and reparation to the victim and the community, incarceration also has the potential to assist at-risk offenders in rehabilitation, potentially leading to a reduction in criminal lifestyle (Bhuller et al., 2020; Hjalmarsson and Lindquist, 2022). As previously discussed, the specific deterrent effect of prison has in general been criticized but prison may for some individuals have a crime-reducing effect beyond incapacitation adding complexity to the matter.

As this study has shown, incarceration does have an incapacitation effect. This is clearly not surprising given that inmates are physically confined to prison. What is notable, however, is that the incapacitation effect found in this study is on average modest, and when categorizing offenders into risk groups, we see substantial heterogeneity. From a policy perspective, the suggested incapacitation effect found for low-risk, first-time incarcerated offenders may still warrant a prison sanction. However, Sweden has one of the highest levels of expenditure per inmate, and the increased use of incarceration has, alongside overcrowding and security issues, raised concerns with regard to fiscal constraints and fears of a deterioration in the capacity to rehabilitate offenders as the number of inmates increases (Kriminalvården, 2022). The somewhat limited crime-preventive effect produced by incapacitating low-risk, first-time incarcerated offenders at least raises the important question of whether noncustodial sanctions might be an alternative for some inmates without giving rise to a risk for substantial costs in terms of recidivism.

Supplemental Material

sj-docx-1-euc-10.1177_14773708241249808 - Supplemental material for Estimating the incapacitation effect among first-time incarcerated offenders

Supplemental material, sj-docx-1-euc-10.1177_14773708241249808 for Estimating the incapacitation effect among first-time incarcerated offenders by Enes Al Weswasi in European Journal of Criminology