The Danish Context
Although the scale and rate of change in the level of community supervision in Denmark is dwarfed by those in the United States, Denmark witnessed a dramatic increase in the use of community supervision over the past 25 years. And, indeed, the number of people under community supervision more than doubled in Denmark from 1985 to 2011, and today 17 per 10,000 of the 5.6 million Danes are under community supervision (compared to 153 people under community supervision per 10,000 of the 315 million Americans). Being a small country with a comparatively low use of community supervision, the absolute increase in the number of people on community supervision was thus small relative to the US, and in Denmark, this number went up from 4,100 in 1985 to 9,300 in 2011—a 128 % increase—compared to an increase from 2.15 million in 1985 to 4.80 million in 2011 in the US, a 124 % increase. The trends in the use of community supervision are hence comparable (in the sense that the percentage change is similar), yet while the change in the US is driven by increases in both probation and parole, the Danish increase is strictly attributable to an increase in the number of probationers.
Unlike the American system, where there is a strict distinction between jail (typically sentences of less than a year) and prison (typically sentences of more than a year) incarceration, the Danish system does not have a strict divide. Sentences in Denmark are generally shorter than in the US, furthermore. As many as 85 % of all sentences in Denmark are shorter than 1 year and <7 % are longer than 2 years (2011 levels). In contrast the mean sentence length in the US is around 4.7 years for federal prisoners (2008–2009 levels) and 2.1 years for state prisoners (Danish Prison and Probation Service 2012a; Guerino, Harrison, and Sabol 2012; Motivans 2012). Despite these differences, putting individuals on probation or parole serves much the same purpose in both countries—to divert individuals who could be sentenced to (or have already served time in) a correctional facility while still keeping them under criminal justice supervision in the hopes of minimizing crime while also minimizing costs.
Prisoners sentenced to more than 3 months of imprisonment in Denmark are expected to achieve early release on parole upon having served two-thirds of their sentence, provided that at least 30 days of the sentence remains to be served. However, to promote order inside the prison and provide an incentive for inmates to use re-socializing initiatives (like pursuing education) while being imprisoned, it is possible to achieve early release on parole after serving half the prison sentence if an inmate shows devotion to achieving re-socialization.Footnote 2 In this sense, the time at which prisoners in Denmark become eligible for parole is not that different than in the United States. Typically, the parole entails a 2 year period during which any violation of the rules that accompany the parole will result in re-imprisonment.
Probation in Denmark, as in the United States, is an alternative to imprisonment that imposes a number of rules and regulations on the offender. For example, during probation an offender might be subject to drug and alcohol tests, restrictions on employment, and unannounced visits to control whether the requirements of the sentence are followed. In Denmark, probations typically entail a 1 or 2 year trial period. By law the probation or parole officer is required to meet with the probationer or parolee every 2 weeks during the first 2 months, and once a month thereafter. At the first meeting—which should take place within the first week following release for parolees, and within the first 2 weeks following conviction for probationers—central aims regarding reintegration should be agreed upon.
There are important differences between the amount of discretion probation and parole officers have in Denmark and in the US. In the US the conditions of probation and parole are often so many that the probation or parole officer could seemingly revoke probation or parole whenever he or she wishes to do so, as there are so many conditions to satisfy that the officer can almost always find some technical violation to report. Probation and parole officers in the US thus have a high amount of discretionary powers. But in Denmark discretion is lower and many rules regulate the supervision that probation and parole officers perform. Probation and parole officers in Denmark do have discretionary powers, for example when they are on a home visit or during meetings with probationers and parolees, but regarding the revocation of probation and parole for technical violations, such a decision has to be validated at court to shield the probationer or parolee against the untimely use of discretionary powers by the probation and parole officers. Also, the central aims of probation and parole in Denmark are, as mentioned, agreed upon during their first meeting, which in turn might lead to fewer revocations. As the amount of discretionary powers assigned to the probation and parole officers is lower in Denmark than in the US, we may assume that probationers and parolees receive more uniform supervision in Denmark, and that the effects of probation and parole officers that we measure in this research article would perhaps be even bigger in a US sample, although this is, of course, an empirical question in need of testing.
The distinction between probation and parole officers is somehow artificial in Denmark, as neither wears a uniform nor carries a gun, and both are more likely to be social workers rather than former police officers. In this sense, we might expect the parole supervision that Danish parolees experience to be similar to what Danish probationers experience. Naturally, this challenges the possibility for generalizing our results regarding Danish parole officers and parolees to American parole officers and parolees, a challenge that we discuss in our conclusion. Yet since both the correlation between probation or parole officer assignment and client outcomes and the causal effect of this assignment on client outcomes has yet to be analyzed, this article makes a significant contribution to the understanding and awareness of the effect of probation and parole officers on their clients, national context notwithstanding.
Most social workers in Denmark supervise both probationers and parolees, and probationers and parolees are subject to the same treatment in terms of control and support as exerted by their probation or parole officer. Therefore—and because probationers and parolees in Copenhagen are assigned to officers following the same rotational assignment process that may be exploited for causal inference, a point we return to—this article assumes the officer fixed effect to remain identical across probationers and parolees once we control for sanction type, probation or parole, and during the course of the article we will refer to probation and parole officers jointly as ‘officers’, and probationers and parolees jointly as ‘clients’.Footnote 3
For this article, we combined data from the Danish Prison and Probation Service with registers of the Danish population, which are available from Statistics Denmark, to produce a unique dataset that allows us to analyze the magnitude of probation and parole officer fixed effects on client outcomes. From the Danish Prison and Probation Service, we obtained unique IDs on all probation and parole officers in Denmark in 2002–2009 along with personal identification numbers on their clients, which makes the clients linkable to the full population registers at Statistics Denmark, which then allowed us to add a range of information on each client both prior to (e.g., controls) and following (e.g., outcomes) supervision.
Our final analytic sample includes 19,534 probationers and parolees along with the 371 probation and parole officers they are assigned to. All supervision cases are initiated and terminated between 2002 and 2009. The raw sample had 53,814 probationers and parolees. We excluded 18,505 drunken drivers, mentally ill offenders, and sexual offenders since such offenders receive their treatment outside the Prison and Probation Service premises and therefore remain unaffected by their probation or parole officer. We have also excluded clients who change their probation or parole officer during their case, as it remains unclear which officer they should be attributed to (which excludes 1,169 cases).Footnote 4 We have further kept only clients younger than 65 years (which excludes 76 clients) and excluded both clients and officers in cases where clients are assigned to officers with less than five total cases over the study period (which excludes 98 officers and 196 cases). Our sample then includes 371 officers who have between 5 and 225 clients, with the mean number of clients being 52.7. A total of 7,245 cases do not match a probation or parole officer and are hence excluded.Footnote 5 For clients with more than one entry during the period (with several separate probation or parole cases over our observation period), we kept only the first entry, to avoid clients receiving multiple treatments (which excludes 3,085 cases). Also, we drop 94 parolees because their initial imprisonment date is earlier than what we have registers available for (see below). The final analytic sample thus includes around 35 % of the raw case stock, yet if we disregard the exclusion of clients who are in fact not treated by probation or parole officers (drunken drivers, mentally ill offenders, and sexual offenders), we still have 55 % of the relevant client stock. Importantly, these 55 % of the relevant client stock are chosen so as to make the sample optimal for analytic purposes and to avoid serial correlation between observations of the same client across different officers.Footnote 6
In line with most studies that investigate the effects of criminal justice supervision, we focus on the effect of officer supervision on labor market outcomes and criminal recidivism. Specifically, we analyze three outcomes, of which two are labor market outcomes and one is criminal recidivism. The labor market outcomes are earnings and the rate of dependency on public benefit transfers. Earnings are measured during the first full calendar year following supervision initiation, and the dependency rate is measured during the first full year following supervision initiation. Specifically, earnings are all wages from legitimate employment, and the rate of dependency on public benefit transfers indicates the share of all weeks during the first year following the week the supervision started that the client received social welfare benefits. Both variables are continuous, yet while earnings is zero or greater for all, the dependency rate falls between zero and one: zero indicates that the client did not receive any subsidized income during the first year since supervision started; one indicates that the client depended on public transfers during all weeks of the first year; and any number in between indicates the share of the first year the client depended on public transfers. Our criminal recidivism outcome measures reconviction during the first two years from the date supervision starts. Criminal recidivism is thus a binary indicator variable taking the value one if a probationer or parole is reconvicted during the follow up period and zero otherwise, with technical violations of probation or parole also included in this measure.Footnote 7
Our main interest is in the individual probation or parole officer’s fixed effect on these outcomes. Typically, fixed effects are used to absorb variance that researchers know is important but are not interested in, as when we, for example, use state or year fixed effects. In our study, however, we are interested in the fixed effects themselves in two ways—what they mean for model fit (e.g., if they improve our predictive power) and how they are distributed (e.g., how exactly they matter).
As mentioned earlier, our data contain unique IDs on all 371 parole and probation officers in the sample, which allows us to model the relationship between each officer and his or her clients’ outcomes. Specifically, we produce a dummy variable for each officer (except one) and enter these into our models. Our reference officer is from Copenhagen and has 104 clients, 70 probationers and 34 parolees, so the reference officer is the same for our analysis of the entire country (where we have 370 dummies) and of Copenhagen (where we have 35 dummies). In the analytic strategy section, we provide a description of our modeling strategy, along with the distinction between the full sample and the Copenhagen sample.
From the register available from Statistics Denmark, we add a range of control variables to our sample of probationers and parolees. First, we add basic information such as age, sex, marital status, whether or not the client has children, how many years of education the client has, and an indicator for ethnic minority background, which indicates whether the individual is an immigrant or the child of an immigrant (relative to being a native Dane). This information is measured just before the supervision is initiated. Second, we add information on the case that the client is under supervision for, namely offense type and trial period, and whether the client is a probationer or a parolee. Third, we add labor market outcomes prior to the case. We add prior earnings measured during the year before supervision for probationers and imprisonment for parolees, and prior dependency on public transfers measured during the year before the date of supervision for probations and imprisonment for parolees.
Notice that we measure prior earnings and prior dependency on public transfers before the parolee’s imprisonment rather than before their parole since we do not expect prison inmates to have earned income nor dependency on public transfers while incarcerated. This, however, means that for some parolees we measure these variables long ago, and since the registers that contain dependency on public transfers exist only from 1985 onwards, we drop parolees imprisoned earlier (which drops only 94 observations). If we were to measure the labor market attachment and income of parolees the year before their parole supervision starts, we would thus get slightly more observations, yet many of these could not be expected to have earned income nor dependency on public transfers due to being imprisoned. Last, we add the number of previous convictions and a dummy indicator for any previous imprisonment.
Table 1 shows descriptive statistics for the full sample and the Copenhagen sample. We show these descriptive statistics on both the full sample and the Copenhagen sample because we only have random assignment of officers to clients in the Copenhagen sample, and only results from this Copenhagen sample are suitable for causal inference. We explain this in detail in the next section.
In the national sample, three out of four are on probation, and the table shows how the probationers and parolees have poor socioeconomic backgrounds. For example, the mean education length is 10.1 years, which is low considering that mandatory education in Denmark is 10 years. The probationers/parolees were on average depending on public benefits 15 % of the year preceding their supervision/imprisonment. The distribution of outcome variables tells the same story, and although the mean earned income during the first full calendar year following supervision is close to DKK 90,000 (which is higher than the mean income before supervision/imprisonment), around 43 % recidivate during the first 24 months following the day their supervision starts—which corresponds to the recidivism rate reported by the Danish Prison and Probation Service (2012b) on probationers and parolees.
In Copenhagen, more clients are on parole, and clients in Copenhagen fare worse in terms of socioeconomic background, which corresponds to anecdotes among the probation and parole officers that the Copenhagen department generally gets worse clients than the rest of the country. Disregarding anecdotes, substantial differences exist between the Copenhagen sample and the national sample.
Finally, we have calculated intra class correlation coefficients for each of the outcomes by officers. These coefficients provide a feel for the amount of variation in the outcome variables that is attributable to the probation and parole officers rather than to the individual clients themselves. These calculations reveal that around 5, 1, and 2.5 % of the variation in earnings, dependency on public benefit transfers, and criminal recidivism is attributable to differences between officers in the national sample, which indicates that officers may matter, whereas the same numbers for the Copenhagen sample are only 0.5, 0.3, and 1.4 %, which indicates that officers may not in fact greatly shape their clients’ outcomes. The discrepancy between the coefficients from the national sample and the Copenhagen sample underlines that severe selection issues contaminate the causal relationship between officers and clients in the national sample, just as it shows that even though probation and parole officers might matter for client outcomes, the causal impact of officers on clients might be less important than common sense and existing studies—which do not have random assignment of officers to clients—directs us to expect.
When data are hierarchical in nature, as in our data where clients are nested within the officers that they are assigned to, it is standard to apply a multilevel model. The main advantage of multilevel modeling is that it allows the researcher to explicitly take into account that observations nested within the same higher-level unit cannot be said to fulfill the assumption of independence that is fundamental to statistical test theory. Since data are hierarchical, the argument goes, each additional observation does not provide a unique additional piece of information, due to the dependency among observations within higher-level units, like officers, and standard errors therefore become too small and it becomes easier to obtain statistical significance. The solution to this caveat would be to explicitly model the deviance between officers as a variance component around the officers’ grand mean—and significant variability between officers would then be interpreted as the distribution of effects of individual officers on their clients.
But even though the multilevel model might be more parsimonious than the fixed effects approach—which is the approach we apply—because fewer parameters are estimated in multilevel models, this comes at the price of precision in estimates. Having less than 50 higher-level observations leads to biased estimates of the higher-level standard errors in both linear (Maas and Hox 2005) and nonlinear multilevel models (Paccagnella 2011), just as higher-level slopes may be unreliable due to influential observations, especially when sample size is low (Van der Meer et al. 2010). As we have only 36 officers in the Copenhagen sample, which we use for causal inference as officers are (almost) randomly assigned to clients in this subsample, we consider the risk of imprecision to be of vital importance.
Our approach is to analyze the effect of probation and parole officers on labor market outcomes and recidivism in five steps. Central to these steps stand our outcome model that regresses the dependent variables on the control variables along with year fixed effects and our explanatory variables of interest, the officer fixed effects. For model diagnostics and interpretations of the individual residual, we estimate the model using OLS with standard errors clustered at the officer level, since this estimator estimates the residual variance from data rather than assuming an error term distribution. However, to avoid predictions outside the [0:1] interval, we use the logit estimator to predict binary outcomes when we apply and interpret model predictions (with standard errors again clustered at the officer level).
The first step is to show that by adding officer fixed effects to the model we improve model fit, which implies that there are systematic differences between client outcomes based on which officer the clients are assigned to. Empirically, we apply two tests of the importance of officer fixed effects. First, we re-estimate the model without the officer fixed effects and use the F-test statistic to test the joint significance of the excluded fixed effects. Second, because the causal relationship between officers and their clients appears to be weak—as was indicated by the low intra class correlation coefficients that we already discussed—we supplement the F-tests with significance tests of the officer fixed effects Partial R-squared, as developed by Shea (1997) and implemented by Davis and Kim (2002).Footnote 8
However, for significant tests to imply the existence of a causal relationship between officer assignment and client outcomes the assignment of officers to clients should be random. In a small country with comparatively few cases of probation and parole, such as Denmark, each officer typically gets all cases within one or more municipalities. Some municipalities are of course larger or have the larger cities in them, and therefore also have more clients and more officers, but generally one or a few officers suffice to perform the needed supervision within municipalities. Because parole and probation officers cannot be randomly assigned in small municipalities, as one and the same officer is assigned to all cases, we cannot differentiate the causal effect of this officer assignment from features of those municipalities. Thus, although analyses of the entire country provide an important first step in considering the effects of probation and parole officers on clients, they cannot provide an uncontaminated estimate of these effects.
In order to deal with this obstacle to causal inference, we show that a rotational officer assignment process in Copenhagen leads to (mostly) random assignment of officers to clients, meaning that estimates from Copenhagen will not be contaminated by endogeneity bias. Here the case and officer stock is greater and whenever a new probation or parole case finds its way to the Copenhagen department, an administrative assistant registers basic information on the case and assigns it to the next officer in line who then receives notification. The administrative assistant does not distinguish between probation and parole cases in her rotational assignment process and she thus assigns both case types to all officers, which is why we do not distinguish between probation officers and parole officers in our analyses.
To show that the Copenhagen rotational assignment indeed randomizes officers to clients, we regress each of the client characteristics on the officer fixed effects, along with year fixed effects. If we do have random assignment of the characteristic in question across officers, an F-test of the joint significance of the officer fixed effects should be statistically insignificant. We also show how the assignment of officers to clients in the national sample (excluding Copenhagen) is far from random. We show this with significant F-tests of the joint significance of officer fixed effects on all client characteristics in a similar model that instead of year fixed effects also includes department fixed effects. While our analysis of Copenhagen allows us to generate an estimate of the effect of probation and parole officers on clients, the national analysis shows results that are hampered by non-random assignment of officers to clients.
The third step of our analysis is to show that in the Copenhagen subsample, where assignment is random, the inclusion of officer fixed effects improves the model fit of our outcome model. We apply the same tests as in the first analytical step.
The fourth step of our analysis moves beyond statistical significance and describes the substantive importance of the officer fixed effects. Here, we consider how the officer fixed effects are distributed by outcome variable, by depicting the prediction of each outcome as it varies by officer. For these predictions, we use a fictional observation that is a probationer with 0 on all binary controls and the Copenhagen subsample mean on all continuous control variables, and we artificially assign this fictional observation to all officers in the sample. We show these results for both the officers in the national sample and the officers in the Copenhagen sample. The graphs from the Copenhagen subsample shows the uncontaminated effects of officers on clients, while the national sample shows estimates hampered by non-random assignment.
The fifth and last step of our analysis investigates whether some officers should be viewed as consistently “good” or “bad” at their job. Put directly, we wish to investigate whether one can extrapolate from the distribution of officer fixed effects on one outcome variable to know whether an officer is generally “good” or “bad” on other outcomes. To investigate this, we calculate the correlation between the different outcome predictions of the fictional observation by which officer he is assigned to. If some officers are consistently “good” or “bad” at their job, this correlation should be sizeable.