Received: 27 April 2018 Revised: 18 October 2019 Accepted: 16 December 2019

DOI: 10.1111/1745-9125.12241

ARTICLE

Long-term consequences of being placed in disciplinary segregation*

Christopher Wildeman1,2 Lars Højsgaard Andersen2

1Department of Policy Analysis and Management, Cornell University, and ROCKWOOL Foundation Research Unit 2ROCKWOOL Foundation Research Unit

Correspondence Abstract Christopher Wildeman, 227C Day Hall, Office Being placed in restrictive housing is considered one of the of the Vice Provost for Research, Cornell University, Ithaca, NY 14853. most devastating experiences a human can endure, yet a Email: [email protected] scant amount of research has been conducted to test how this experience affects core indicators of prisoner reentry Funding information Rockwool Foundation such as employment and recidivism. In this article, we use Danish registry data, which allow for us to link penal con- ∗ Additional supporting information ditions to postrelease outcomes, to show how the reentry can be found in the full text tab for this article in the Wiley Online Library at outcomes of individuals placed in disciplinary segregation, http://onlinelibrary.wiley.com/doi/10.1111/ which is placement in restrictive housing because of disci- crim.2020.58.issue-3/issuetoc. plinary infractions, compare with those sanctioned for in- The authors would like to thank the anonymous Criminology reviewers and Co-Editor Brian D. prison offenses but not placed in segregation. The results Johnson for their helpful feedback. The authors from matched difference-in-differences analyses show that thank the ROCKWOOL Foundation for pro- Danish inmates placed in disciplinary segregation experi- viding funding. Sara Wakefield, Chris Muller, Andy Papachristos, and seminar participants ence larger drops in employment and larger increases in at Cornell University, Princeton University, the risk of being convicted of a new crime in the 3 years the University of California—Berkeley, the after release from a correctional facility than do Danish University of Chicago, Duke University, the University of North Carolina, the University of inmates who were sanctioned for a serious offense but not Texas, Vanderbilt University, and Washington placed in disciplinary segregation as a result. Because being University—St. Louis provided excellent feed- placed in disciplinary segregation, and restrictive housing back on an earlier draft of this article (or on a presentation of it). more broadly, is so common, these results indicate that restrictive housing placement may be a key moderator of the effects of incarceration that merits more attention from criminologists, provided the associations shown here rep- resent causal effects and generalize.

This is an open access article under the terms of the Creative Commons Attribution License, which permits use, distribution and reproduction in any medium, provided the original work is properly cited. © 2020 The Authors. Criminology published by Wiley Periodicals, Inc. on behalf of American Society of Criminology

Criminology. 2020;58:423–453. wileyonlinelibrary.com/journal/crim 423 424 WILDEMAN AND ANDERSEN

KEYWORDS incarceration, inequality, registry data, restrictive housing, solitary confinement

By all accounts, being in restrictive housing1 is an extreme experience. Inmates who are placed in restrictive housing exist in solitude for all but (at most) 1 to 2 hours per day and complete all activities, with the possible exceptions of bathing and taking exercise, in their cells (e.g., Haney, 2018; Kapoor & Trestman, 2016, p. 200; Mears et al., 2019). Restrictive housing generally takes one of three forms: 1) administrative segregation, 2) disciplinary segregation, or 3) protective custody. Administrative segregation often maps on to modern conceptions of the “supermax” prison (e.g., Haney, 2018; Reiter, 2016). Rather than being linked with specific dis- ciplinary infractions that take place in prison, inmates in administrative segregation are placed there over concerns about their capacity to cause disruption, especially violent disruption, within the com- munity.2 Although estimating exposure to restrictive housing and the share of inmates placed in dif- ferent types of restrictive housing is inordinately difficult because of data limitations, inmates placed in administrative segregation almost certainly experience the greatest exposure to restrictive housing, sometimes stretching to years or even decades. They are also probably most likely to remain in prison for the remainder of their lives. In addition to the three forms, which represent the formal versions of restrictive housing, informal restrictive housing may also occur, in which inmates are de facto confined in solitude yet are just not recorded or counted as such. Long durations in restrictive housing and low reentry rates to general society may be normal out- comes for inmates in administration segregation, but inmates placed in disciplinary segregation and protective custody likely have shorter stays in restrictive housing and are more likely to reenter society. Inmates in disciplinary segregation are in restrictive housing as a sanction for disciplinary infractions; protective custody is used when inmates request isolation for protection or are perceived by officials to need to be kept in isolation for protection. Academic research on restrictive housing has generally taken four forms. The first has been focused on the ethics of restrictive housing placement, with restrictive housing—more often called “solitary confinement “in this literature—considered to be cruel and unusual punishment that must be abolished (e.g., Bennion, 2015; Gawande, 2009). The second, which is related but more empirical, has been focused on the consequences of exposure to restrictive housing—often extremely long exposure in “supermax” facilities—for the mental health of inmates. Although some working in this area have claimed that there is definitive evidence that restrictive housing damages—or even destroys—mental health (e.g., Haney, 2018), others have argued that the lack of appropriate data makes it difficult to determine exactly how, if at all, restrictive housing placement affects mental health (e.g., Kapoor & Trestman, 2016; Labrecque, 2016; Morgan et al., 2016). The third form has been focused on how restrictive housing placement rates affect rates of violence against inmates and staff in the facility (e.g., Briggs, Sundt, & Castellano, 2003) and on how placement in restrictive housing affects the probability of future infractions (e.g., Labrecque & Smith, 2019; Morris, 2016). As such, the third area of research has been broadly aimed at how restrictive housing affects safety and security in facilities, an issue that is obviously of the utmost importance to those working in corrections. A fourth and final area has been focused on how placement in restrictive housing affects postrelease outcomes, with special attention on recidivism (e.g., Butlter, Steiner, Makarios, & Travis, 2019; Mears & Bales, 2009). Although prisoner

1We use the term “restrictive housing” rather than the terms “solitary confinement” or “the hole.” 2Of course, in-prison infractions could also play a role in placement in administrative segregation. WILDEMAN AND ANDERSEN 425 reentry is common among inmates who spend time in restrictive housing, this area is probably the smallest of the four, and the methods used to this point, propensity score matching in one case and covariate adjustment in another, are a significant limitation. This relative inattention to the long-term consequences of placement in restrictive housing is unfor- tunate for several reasons. First, if the often-extreme psychological difficulties that result from being placed in restrictive housing are indeed a result of that experience, these difficulties are likely to spill out to other domains, making it difficult for inmates to refrain from criminal activity, gain and maintain employment, and prosocially engage with society (Andersen, 2004; Gordon, 2013; Grassian, 2006; Haney, 2003; Smith, 2006). Given how well documented the effects of mental health are on labor market outcomes (e.g., Ettner, Frank, & Kessler, 1997) and criminal activity (e.g., Moffitt, 1993), moreover, it is reasonable to expect long-term consequences of restrictive housing placement on these broader outcomes, assuming, again, a causal effect on mental health. Second, knowing how restrictive housing placement affects former inmates’ outcomes not just in terms of mental health but also in other domains provides a more complete assessment of the positive and negative long-term consequences of restrictive housing than we currently have. As a large number of inmates cycle through restrictive hous- ing each year, this is not merely an academic concern as better identifying its consequences provides insights into how one prevalent condition of confinement affects how former prisoners fare. Despite the importance of testing the long-term consequences of restrictive housing placement,3 doing so is exceptionally difficult because it requires 1) information on inmates who are placed in restrictive housing, as well as on those who are not; 2) linking with information on core postrelease outcomes and preadmission outcomes; and 3) low levels of attrition. Each of these conditions in and of itself would represent challenges as the number of studies using data including any information on prison conditions (e.g., Kreager et al., 2016), linking administrative data on prisoners to their postre- lease outcomes (e.g., Loeffler, 2013) or having low attrition among this population (e.g., Western, Braga, Hureau, & Sirois, 2016), is minimal. And, as such, it is unsurprising that we know of no other data set that can be used to test the long-term effects of being placed in restrictive housing on former inmates’ broad postrelease outcomes, although some existing data have been linked to recidivism (e.g., Butlter et al., 2019; Mears & Bales, 2009). To circumvent these problems, we use a unique data set that combines two administrative data sources: 1) Danish registry data and 2) data from the Danish Prison and Probation Service, which includes controls for prior contact with the criminal justice system, as well as information on restrictive housing placement, other recorded in-prison sanctions, and convictions. We focus on employment and conviction because they are central indicators of how successful prisoner reentry has been and because so much research on the consequences of incarceration has been focused on them (e.g., Petersilia, 2003; Travis, 2005; Western, 2006; Western, Braga, Davis, & Sirois, 2015). We focus on short-term stints in disciplinary segregation because these are the inmates who are most likely to be exposed to restric- tive housing and then released into society only shortly thereafter. These unique data allow for us to use a difference-in-differences model to provide the most rigorous test to date of the consequences of restrictive housing placement for post-release outcomes.

1 SHORT-TERM RESTRICTIVE HOUSING PLACEMENT AND PRISONER REENTRY

There are a host of reasons to expect inmates who are placed in restrictive housing for even short stints of time for disciplinary infractions to fare poorly in terms of reentry outcomes once they are released

3Many of these issues also apply to testing the short-term consequences of restrictive housing placement. 426 WILDEMAN AND ANDERSEN from a correctional institution. In this section, we highlight three avenues through which even short exposures to disciplinary segregation could lead to poor reentry outcomes, as well as highlight why selection into restrictive housing could also drive these poor outcomes. Probably the most likely channel through which restrictive housing placement could shape reentry outcomes is through long-term consequences for mental health. Although data limitations make it difficult to establish with certainty that restrictive housing placement harms mental health (e.g., Kapoor & Trestman, 2016; Labrecque, 2016; Morgan et al., 2016), the findings from a large body of research do indicate that restrictive housing placement may do serious psychological harm to inmates (e.g., Andersen, 2004; Cloud, Drucker, Browne, & Parsons, 2015; Gawande, 2009; Grassian, 2006; Guenther, 2013; Haney, 2003, 2018; Reiter, 2016; Smith, 2006). During the time that inmates are in restrictive housing, they experience a range of problems including trouble sleeping, impaired concentration, lethargy, irrational anger, depression, hallucinations, and suicidal ideation and suicide attempts (Andersen, Sestoft, Lillebaek, Gabrielsen, & Kramp, 1996; Haney & Lynch, 1997; Kaba et al., 2014; Kupers, 1999; Rhodes, 2004). Although many of these problems increase with time in isolation, some scholars have argued that profound psychological trauma can begin even a few days after being placed in restrictive housing.4 And for many, these effects do not fully dissipate after their release from restrictive housing, leading to poor mental health months and even years into the future (Andersen, 2004; Grassian, 2006; Haney, 2003; Smith, 2006; but see Kapoor & Trestman, 2016).5 Because poor mental health is strongly linked in the general population with poor labor market outcomes (e.g., Ettner et al., 1997) and criminal activity (e.g., Moffitt, 1993), any effects of restrictive housing placement on long-term mental health could impede prisoner reentry. Although poor mental health is likely the key causal driver of the poor reentry outcomes of inmates who spend time in restrictive housing, there are at least two other channels through which restrictive housing placement could impede reentry: 1) disruptions to programming and 2) being labeled a “prob- lem inmate” by staff. Of course, for disruptions to programming to matter for reentry, we would need to know with some degree of certainty that the programming would have improved outcomes absent a disruption. Unfortunately, the evidence from the prisoner reentry programs literature is far from so clear-cut (e.g., Jonson & Cullen, 2015). Despite this mixed evidence in regard to the efficacy of pris- oner reentry programs, inmates who experienced a disruption to programming as a result of restrictive housing placement could experience worse outcomes than they would have had they not experienced this disruption. A final causal mechanism potentially leading restrictive housing placement to poor reentry outcomes builds on labelling theory (Becker, 1963/1997), arguing that placement leads to inmates acquiring the “bad inmate” label in the eyes of correctional staff, leading to a vicious cycle of poor treatment at the hands of the guards and worsening in-prison outcomes for the inmate. Although little evidence to this effect exists within research on restrictive housing—a reasonable omission given the relative lack of qualitative evidence around shorter stays in solitary—the findings from research on exclusionary school discipline, in which a strong parallel is provided in many regards, indicates that processes along these lines may play out (Jacobsen, Pace, & Ramirez, 2019).

4As Koch (2014, pp. 101–102) noted, “[S]ymptoms often occur after only a few days. Most common are problems of concen- tration, restlessness, failure of memory, sleeping problems, and impaired sense of time and ability to follow the rhythm of day and night. … Nightmares and anxiety are very common. … Suicide attempts are often made.” 5As Haney (2018, p. 297) noted, “Prisoners may develop extreme habits, tendencies, perspectives, and beliefs that are difficult or impossible for them to relinquish once they are released. Although their adaptations may have been functional under condition of isolation … they are highly dysfunctional in the social world most prisoners … re-enter.” WILDEMAN AND ANDERSEN 427

Of course, plausible though each of these mechanisms may be, the reality is that selection into restric- tive housing rather than a causal effect of placement into it may be driving any differences in reentry outcomes we observe. Whether the sample is inmates in “supermax” facilities (e.g., Mears & Bales, 2009, p. 1149) or those placed in disciplinary segregation (e.g., Morris, 2016, p. 12), there are marked differences between those who do and do not experience restrictive housing placement that could act as confounders. As such, even though existing research findings indicate—sometimes strongly and some- times tentatively—that restrictive housing placement could lead to poor reentry outcomes, any study of this subject must deal with a host of potential confounders in a rigorous way that moves beyond adjusting for observables.

2 RESTRICTIVE HOUSING AND IMPRISONMENT IN DENMARK

2.1 Experience of being in restrictive housing in Denmark In the Danish context, disciplinary infractions that can lead to disciplinary segregation include the following: escape or attempted escape; possession of contraband, such as alcohol, drugs, or weapons; refusing to provide a urine sample for alcohol and drug testing; violent behavior (or the threat hereof) toward inmates or staff; vandalism; and other serious and repeated infractions. In Denmark, disciplinary segregation cannot exceed 4 consecutive weeks for any offense. Restrictive housing in Denmark takes place in one of five types of cells, reflecting similar hetero- geneity in restricting housing as other contexts (Kapoor & Trestman, 2016): 1) a cell in an adminis- trative segregation unit; 2) the inmate’s cell; 3) a cell in a local jail; 4) an observation cell (with little inside of it, all of which is nailed to the floor); or 5) a security cell (which only contains a bed that may be used for restraining the prisoner using belts and foot-straps). Observation and security cells are only used for the most severe cases; prison staff are required to observe the prisoners placed here at regular intervals (Langsted, Garde, & Greve, 2011). Danish accounts of being in restrictive housing are admittedly somewhat limited, but anecdotal and qualitative evidence reveals that the experience is much the same in Denmark as it is in most other developed democracies (e.g., Koch, 2014; Smith, 2006). In qualitative research, Minke (2012) described the administrative segregation unit of one of the high-security (closed) Danish prisons. This unit is known among prisoners as “the hole,” which is language that is consistent with how restrictive housing is discussed in the United States (and elsewhere). It is silent, and all doors are always locked. Cells are approximately 86 square feet, and they have wire mesh in front of the window. As is the case with restrictive housing more broadly, inmates are kept in their cell 22–23 hours per day. The walls are undecorated, and there is minimal furniture. Outside each cell door there is a blackboard with the prisoner’s ID number written on it in chalk along with a note on the reason for being placed there. Other prisoners who are also placed in the unit can observe this information when they leave their cell for exercise, which also takes place in solitude in a separate small yard that has bars or wire mesh as a roof.

2.2 Prevalence and duration of restrictive housing in Denmark To show how common punishment cell confinement is in Denmark, we used data on all Danes who experienced incarceration from 2006 to 2013 (more on this later). The Danish data only include infor- mation on punishment cell placement, not other types of disciplinary segregation (such as security cell placement or de facto but unrecorded segregation, or the like). Prevalence estimates for Denmark must hence be considered lower bound etimates of the total prevalence of disciplinary segregation in 428 WILDEMAN AND ANDERSEN

TABLE 1 Restrictive housing in the United States, 2011–2012, and Denmark, 2006–2013 (Denmark N = 7,821,294 person-days; U.S. N = 91,177) Denmark United States Closed Prisons Open Prisons Jails Prisons Jails In Restrictive Housing Last Night (%) Yes .680 .565 .595 1.900 2.200 No 99.320 99.435 99.405 95.600 93.300 Don’t Know .000 .000 .000 2.500 .500 In Restrictive Housing in Last 12 Months, by Time Since Admission (%) All 15.143 8.774 14.483 18.100 17.400 <1 Month 3.055 1.359 1.576 8.400 8.000 2–3 Months 9.158 6.342 6.575 11.600 14.300 4–5 Months 17.422 14.178 15.327 13.500 19.600 6–8 Months 25.735 21.402 23.850 19.800 27.300 9–11 Months 32.384 28.571 32.429 22.000 32.200 12+ Months 23.520 18.018 22.708 20.400 35.400 Average Exposure in the Last 12 .150 .087 .144 .086 .035 Months (Months) In Restrictive Housing in Last 12 Months, by Offense Type (%) Violent Sex Offense 3.488 3.341 7.826 15.500 20.500 Other Violent Offense 21.368 11.325 20.573 24.600 27.700 Property Offense 25.749 14.082 17.002 19.100 18.000 Drug Offense 15.814 12.241 15.071 14.400 15.600 Other Offense 22.442 11.282 16.233 15.200 13.500 Number of Days in Restrictive Housing in Last 12 Months (%) 0 79.811 88.165 82.689 79.300 82.200 ≤1 .924 .453 .548 .600 1.600 2–6 13.280 8.212 11.933 2.200 4.000 7–13 5.234 2.780 4.320 2.400 3.100 14–29 .458 .203 .318 3.400 3.100 30+ .294 .187 .193 2.600 5.400 Don’t Know .000 .000 .000 2.600 .500 Notes: The Denmark data are a repeated daily cross-sectional dataset made from all incarceration spells in 2006–2013 (N = 7,821,294 person-days). All spells were followed until terminated or, for those extending beyond this date, to December 31st, 2013. The figures in this table thus report the shares of all person-days incarcerated during this time window that were served in restrictive housing. During our data window, three Danish prisons had both closed and open prison wings, yet because the capacity in these open wings exceeds the capacity in the closed wings in each of the three prisons, all incarceration spells from these prisons are recorded in the open prison category. The estimates from the United States are based on data from the National Inmate Survey (N = 91,177) from 2011–2012 and have been published in previous research (Beck, 2015).

Denmark. To provide some context into how these rates of punishment cell confinement compare with the total rate of placement in restrictive housing in other contexts, table 1 provides a comparison of the Danish results for punishment cell confinement with the results based on surveys of all restrictive housing placement during the years 2011–2012 in the United States (Beck, 2015). We do not refer to the U.S.-specific findings until we reach the Discussion and Conclusion section. WILDEMAN AND ANDERSEN 429

In Denmark, approximately 0.6 percent of inmates across all facility types were in a punishment cell last night. Although few Danish inmates are in a punishment cell on any given night, many will be placed in a punishment cell at some point. An estimated 15.1 percent of Danes who were initially admitted to a closed prison were placed in punishment cell in the last year, and Danes in local jails and closed prisons also experienced this event at high rates. As table 1 also shows, stays in a punishment cell tend to be short. Only .75 percent of Danish inmates in closed prisons have ever been placed in punishment cell for more than 2 weeks, for instance, with Danish inmates in open prisons and local jails experiencing this duration of exposure at even lower rates than that. Thus, placement in a punishment cell in Denmark is common but tends to be brief.

2.3 Prisons, imprisonment, and the release process in Denmark Although there are many core ways in which the purpose and experience of restrictive housing align in Denmark and other developed democracies, there are important differences between the correctional system in Denmark and elsewhere. The first two of these differences relate to the experience of restric- tive housing, and the remaining differences relate to how prison and jail incarceration and the release process in Denmark more broadly differs from other contexts. First, there are no Danish “supermax” prisons. This difference is critical because most existing research on the consequences of restrictive housing has been focused not on inmates who are in restric- tive housing for short periods of time but on those in long-term restrictive housing, many of whom are in solitary confinement for the duration of their sentence (Briggs et al., 2003; Haney, 2003; O’Keefe et al., 2013; Shalev, 2009; Toch, 2007/1975; Travis et al., 2014, pp. 183–188; Zinger, Wichmann, & Andrews, 2001; but see Morris, 2016; Useem & Piehl, 2006). Our analyses relate not to this group but to inmates who are usually in the general penal population and will be in a correctional facility for a year or two. We see this as a benefit of our study as these are the inmates who will be back in society in short order and, hence, whose adjustment to post-prison life is substantively and theoretically inter- esting. Indeed, sentences in Denmark are so short that most inmates fall into this category: Denmark has one of the lowest incarceration rates in the world, and close to 60 percent of sentences are shorter than 4 months. The shortest prison sentences in Denmark are 7 days long (Danish Prison & Probation Service, 2018; Walmsley, 2018). Second, Danes who are detained pretrial spend practically all of their time in restrictive housing. This has been standard practice in Denmark for decades, a practice that has repeatedly been criticized by international human rights organizations (e.g., Engbo & Smith, 2012). There are two reasons pre- trial detainees are effectively placed under restrictive housing conditions, namely, 1) pretrial detainees are kept in local jails, which simply do not have the facilities required to establish prison commu- nities (they consist of a handful of cells with no common areas and only a small outside area), and 2) pretrial detainees in Denmark are not allowed to communicate with one another because of the risk of collusion. Detainees placed in local jails in Denmark only have the right to 1 hour of outdoor exercise per day, and they often have restricted visitation, mail, and phone calls. In addition to host- ing pretrial detainees, local jails in Denmark also host postconviction prisoners who serve very short sentences. Third, Danish prison law is based on the “principle of normalization,” which means that no restric- tions are placed on inmates unless deemed necessary to prevent escape from the prison or to keep order in the prison (Langsted et al., 2011). Prisoners have the same civil rights as other citizens both during and after imprisonment. Time spent in prison is meant to resemble normal life on the outside, which includes adhering to a workday schedule (8 hours of sleep; 8 hours of employment, training, or educa- tion; and 8 hours of leisure activities). Prisoners are paid for their work, although at a lower wage than 430 WILDEMAN AND ANDERSEN in society, and they use this income to buy groceries in an in-prison store (they cook their own meals in prison wing kitchens). Fourth, prisoners have the right to serve the sentence in an open prison unless circumstances speak against it (circumstances include high risk of escape, the offender being dangerous to other inmates, and sentence length). In open prisons, doors are not locked, the prison is surrounded by a fence, and the staff-to-inmate ratio is just below 1:1. There is strong focus on resocialization, and some inmates are—provided that they are found eligible for it by the prison board—even allowed to fulfill their daily 8 hours of work or schooling outside the prison if a specific program that is especially central to the inmate’s resocialization is unavailable in the prison. The inmate may pursue such programs unaccompanied, and such inmates thus only spend evenings and nights in prison. The inmate capacity in open prisons in Denmark was 1,115 at the end of 2017 (Danish Prison and Probation Service, 2018). Inmates who are not placed in open prisons are placed either in local jails or in closed prisons. Sentences longer than 5 years, which are extremely rare in Denmark, automatically send the inmate to a closed prison. Closed prisons are much more restrictive than open ones: Doors are locked, and the prison is surrounded by a concrete wall. The inmate capacity in closed prisons in Denmark was 895 at the end of 2017, and the staff-to-inmate ratio is just above 1:1 (Danish Prison and Probation Service, 2018). Employment, training, or education is only allowed within the prison, and prisoners in closed prisons are not allowed to leave the prison premises unless a board strictly permits it (and if permission to leave the prison was granted, this would be in the company of a prison guard). Fifth, the release process in Denmark differs from other contexts too. Prison staff are required to fill out a document describing the prisoner’s life situation, resources, and challenges, and specifying the expected timing of the sentence and release process (Engbo, 2009). To secure consistency, the document follows the prisoner throughout the entire sentence. In principle, the document only has to be filled out for prisoners serving sentences longer than 4 months, but because there are many excep- tions to this rule, the plans are filled out for far more prisoners (Rasmussen & Ramsbøl, 2009). The plan—which must be filled out no less than 4 weeks after admission—is regularly updated to fit the prisoner’s situation and the progress of the sentence. As release approaches, either by time served or by early release on parole, the document becomes the key coordinator of how the release process should be structured and how the prisoner is handed over from the prison system to social services. Regarding the release process, the plan details when supervised and unsupervised weekend leaves from prison may be obtained, whether and when the prisoner should expect to be released to a halfway house, and so forth. Regarding the cooperation with social services, Denmark has had guidelines for this since 1998, which were passed into law in 2006. During our data period, prison staff are thus required to inform social services about the inmate’s resources and challenges to secure faster assistance to the released prisoner in the community. Early release on parole is expected after having served two thirds of the sen- tence, provided that the sentence was longer than 3 months. If refused, a prisoner may demand a court hearing. If the prisoner has good resocialization offers available or if, for example, humanitarian or health issues speak for it, early release on parole may be granted after having served half the sentence. For prisoners who serve long sentences (which in Denmark means having served at least 4 months in prison at the time of filing the parole request), release after half time can be achieved if the prisoner has been extraordinarily devoted to achieving resocialization (by taking part in, for example, treatment). Restrictive housing, imprisonment, and the release process in Denmark thus differ from most other contexts. Most importantly for this article, the differences imply that although Danish closed prisons constitute the most directly comparable case to prisons in other and more punitive contexts, this com- parability only concerns material aspects (levels of security and the types of restrictions that are put on inmates) of the prisons, not the prison population. This is because most inmates in Denmark are placed in open prisons, reserving closed prisons only to those with very long sentences (relative to WILDEMAN AND ANDERSEN 431

Danish sentences) and those with a high risk of escape. The population in closed prisons in Denmark is, in effect, highly selective and is not indicative of the general prison population in Denmark. The same argument also applies to local jails in Denmark as they host inmates serving very short sentences and under conditions that resemble restrictive housing. Our solution to these challenges of comparing results from Denmark to other contexts is to lay out results for all three types of correctional facilities, allowing us to compare associations between being placed in punishment cell and postrelease outcomes across all three facility types.

3 DATA, MEASURES, AND ANALYTIC STRATEGY

3.1 Data In this study, we rely on two sources of Danish administrative data. First, we rely on registry data (Andersen, 2018). There are three key features of these data for our analyses. First, they include infor- mation on the entire population of Danes. Especially in this area, where attrition rates tend to be high (e.g., Wakefield & Wildeman, 2013; Western, 2002), this is no small benefit. Second, the data include a rich set of information about the family life, educational background, mental health, employment history, and criminal history of the population. Finally, the data can be linked to other data sets with the Danish equivalent of a U.S. social security number. The second data set includes information on all prisoners from 2006 to 2013. From these data, we keep all spells of imprisonment that started in 2006 or later and that had ended by the end of 2013. For the purposes of our analyses, a couple of components of the data merit attention. First, because the data include information on where each inmate was each day, we can precisely measure the duration of punishment cell confinement for each inmate who were recorded as having experienced it. Second, the data include information on all infractions that individuals were formally sanctioned for while incarcerated. And, as such, the data allow for us to consider three distinct types of inmates: 1) those who were never officially sanctioned for their behavior while incarcerated; 2) those who were officially sanctioned but never placed in a punishment cell; and 3) those who were formally sanctioned and placed in a punishment cell. This unique feature of the data can be used to facilitate our analysis, allowing us to compare inmates who are recorded as having been placed in punishment cell for violating the rules in prison with the majority of the prison population that are not recorded with any in-prison sanctions, as well as with inmates who are recorded as having received some sort of sanction but who were not placed in a punishment cell. We restrict our analyses in this article to the last two groups because prisoners who were never officially sanctioned for disciplinary infractions differ so markedly from the other two groups on a range of observed and likely also unobserved characteristics, making it unclear whether comparisons would be appropriate even with extensive matching of groups. Throughout this article, when we refer to our comparison groups, we strictly refer to inmates who are recorded as having had these experiences. They may thus have experienced other but unrecorded types of sanctions. This type of measurement error, however, will most likely bias our estimates downward (some people in the control group may have experienced harsher sanctions than what is recorded), implying that our significant findings stand out as even stronger. Of course, it could be the case that inmates who were placed in a punishment cell and who were given other sanctions committed different types of infractions while in captivity. If that were the case, we might expect our lack of individual-level information on the reason for being punished for an in- prison infraction to be problematic. As table 2, which includes aggregate data on in-prison infractions that resulted in punishment cell placement or some other sanction, indicates, there are some differences between these two groups in terms of infraction type. Interestingly, with the exception of violations of 432 WILDEMAN AND ANDERSEN

TABLE 2 Distribution of infractions by sanction type, percent, 2006–2013 (N = 130,388) Infraction Punishment Cell Other Sanction Total Refused drug test 5.762 10.904 10.073 Refused employment .906 1.729 1.596 Possessing drugs/weapons 13.220 20.467 19.297 Opposed staff instructions 5.868 6.432 6.341 Attempted escape 1.331 .452 .594 Possessing illegal goods 41.571 34.236 35.421 Failure to return from leave .512 .649 .627 Other infractions during leave 2.376 4.663 4.293 Violating the penal code 13.158 2.675 4.368 Violating facility-specific rules 15.296 17.793 17.389 Percentage of sanction type 100.000 100.000 100.000 Percentage of all infractions 16.154 83.846 100.000 Notes: From 2006 to 2013 the official total number of punish cell placement spells was N = 21,062 and the number of other sanctions was N = 109,326. These total numbers include infractions committed during pretrial detention. Source: Danish Prison and Probation Service (2007–2014). the penal code, which make up a small share of all offenses (4.4 percent), the largest differences are found for possessing illegal drugs and weapons—with 13.2 percent of those placed in a punishment cell committing this offense and 20.5 percent of those with other sanctions committing this offense—and possessing other illegal goods, most often cell phones—with 41.6 percent of those in a punishment cell committing this offense and 34.2 percent of those with other sanctions committing this offense. When combined, these categories make up 54.8 percent of the cases with punishment cell confinement and 54.7 percent of cases that received other formal sanctions. When combined with the small differences across other categories, it would be reasonable to conclude that the inmates in these groups are not committing fundamentally different infractions. Although no data exist on the relationship between infraction type and length of punishment cell con- finement, through personal correspondence with the Danish Prison and Probation Service, we learned that there is vast heterogeneity in the length of restrictive housing imposed for specific offenses. And even though some offenses, such as violence and threats, tend to bring longer stays in restrictive hous- ing (sometimes in excess of a week), more seemingly minor offenses can also bring quite long stints in restrictive housing. Refusing a drug test, for instance, comes with a standard 5 days in restrictive housing. And being caught with a cell phone for a third time in a closed prison comes with a mandatory sentence of 28 days in restrictive housing.

3.2 Measures Using these two data sets, we construct our dependent, explanatory, and control variables. Our key dependent variables are criminal conviction and employment.

3.2.1 Criminal conviction We obtain criminal convictions from official court transcripts which include information on offense dates, allowing us to focus on the timing of offenses that result in prosecution and conviction. With these official conviction data, we observe whether (0 = “No”, 1 = “Yes”) each person in the data was convicted of violating the penal code within a window of 2–3 years before imprisonment and 3 years WILDEMAN AND ANDERSEN 433 after release from prison. We do not include offenses committed during the last year before impris- onment in our preadmission measure as offenses at this point are likely to be treated as co-offenses to the case that eventually sent the offenders to prison (and, as a result, offenses in this time window could thus be endogenous to the imprisonment we observe). The main advantages of using conviction data concern their administrative nature: By covering the full pool of convictions in Denmark, these data do not suffer from any of the biases that other data sources may suffer from. But, notably, the key limitation of using official conviction data also concerns their administrative nature: By focusing only on cases which lead to formal court proceedings, we effectively analyze what Bushway and Tahamont (2016) referred to as “criminal justice careers,” not criminal behavior. Considering racial, ethnic, gen- der, and social class disparities in the risk of being processed by the criminal justice system, this is no small limitation. We acknowledge that supplementing our results with analyses based on other data sources, such as self-reports, would enhance the validity of our conclusions. A lack of survey data on the Danish population or even a sample, however, forces us to invite future studies to be designed to replicate our results using such other data sources. Although we could have also considered incarceration as an outcome, we focus on new convictions only because we see this as a more appropriate gauge of recidivism than being picked up for technical violations of parole. We also run supplementary analyses in the online supporting information that instead were aimed at considering arrest as well as any new incarceration (arrest, pretrial detention, or postconviction incarceration); these results yield estimates comparable with those herein, a point we return to.6

3.2.2 Employment We obtain employment information from official tax records. In Denmark, there is full third-party reporting of income to the tax authorities—employers are required to report salaries, fringes, bonuses, severance pays, board fees, stock options, salaries during leave, and even nontaxable salaries directly to the tax authorities—and any income from legal labor work is thus counted on these records. With these records, we observe whether (0 = “No”, 1 = “Yes”) each person in the data had any income from employment in the formal labor market before and after imprisonment. Because tax records are filed annually, we cannot identify with certainty whether formal labor income during the year when imprisonment occurs was generated before or after the imprisonment spell. Therefore, we divide annual labor income by 12 to obtain average monthly labor income within years, and we then ignore average labor income during the last 11 months before imprisonment and the first 11 months after release from prison. Doing so ensures that we do not conflate the timing of income with the timing of imprison- ment but maintain a balanced data structure. Just as was the case for criminal convictions, one obvi- ous and important limitation of using tax records for measuring employment concerns the data being administratively defined: These data only include earnings from legal work. Income from black mar- ket activity—such as income from crimes or from other sources that remain off the books—are not covered, which is unfortunate because one could imagine such income playing an important role for prisoners once they are released. Black market activity is risky, however, and for most people “work- ing” in that arena, earnings are low (Levitt & Venkatesh, 2000). Again, we invite future studies to be designed to replicate our findings using other data that have access to all kinds of earnings and employ- ment, yet our focus on resocialization (which would seem to have better stakes in the formal than in the informal labor market) and the lack of linkable population surveys concerning black market activities makes us focus exclusively on administrative data in our analyses.

6Additional supporting information can be found in the full text tab for this article in the Wiley Online Library at http://online library.wiley.com/doi/10.1111/crim.2020.58.issue-3/issuetoc. 434 WILDEMAN AND ANDERSEN

FIGURE 1 Probability of conviction and employment before and after incarceration. Denmark, 2006–2013 (N = 36,360) Note: Figure shows results for all facilities. For separate results by facility type, see figure A1. Source: Own calculations based on data from Statistics Denmark.

Figure 1 presents descriptive statistics of our main outcome variables for the pooled data of all facilities (results by closed prisons, open prisons, and jails are presented in figure A1).

3.2.3 Explanatory variable Our explanatory variable is whether each inmate was recorded as having experienced (1) punishment cell confinement or (0) other disciplinary actions. Other types of disciplinary actions include fines, warnings, conditional solitary confinement, and the confiscation of contraband (Langsted et al., 2011). As mentioned, we define the groups from official records, implying that other and unrecorded sanc- tions may also have occurred. Table 3 displays descriptive statistics on the share and characteristics of inmates split by the key explanatory variable. Table 3 also provides descriptive statistics on the general prison population who were not recorded as having experienced any sanctions, simply to pro- vide a feeling for how select prisoners who are recorded with disciplinary actions are relative to other prisoners.

3.2.4 Control variables All analyses also include a host of controls. Most of these are listed in table 3; all controls are described more in the online supporting information. The control variables include an array of information about the inmates, including age, gender, and other demographic controls, such as parental information; their prior contact with the mental health care system (defined as whether they were referred by their general WILDEMAN AND ANDERSEN 435 physician to the mental health care system and used the referral); and whether they had experienced any incarceration before the current one (0 = “No”, 1 = “Yes”); as well as information about their criminal history and the case for which they are serving a prison sentence. Specifically, we control for whether the incarceration spell is the person’s first, second, or third or more spell in the data, admission and release year, whether he or she was detained pretrial, sentence length and length of incarceration, crime type, frequency and type of recorded nonsolitary disciplinary actions, and whether the inmate was first assigned to a closed prison, an open prison, or a local jail. As we noted in table 1, these distinctions are essential given the different rates of punishment cell confinement across facility type. The table also reports levels of the main as well as alternative outcome variables both before and after the sentence. As is clear from these descriptive statistics, inmates who were placed in a punishment cell are more similar to those who were recorded with other sanctions than those who were not. Nonetheless important differences between these two groups are still observable, which we aim to take into account in our analytic strategy.

3.3 Analytic strategy We run analyses using both the pooled data for all facilities and separately for each facility type (closed prisons, open prisons, local jails, referring to the facility type the prisoner was first assigned to). But to keep this section concise, we explain the model, the main analysis, and the supplemental analyses in online supporting information in general terms based on a pooled model. The same logic applies to the analyses for each facility type, and the only difference is that unobserved heterogeneity is likely to be smaller when “zooming in” on specific facility types.

3.3.1 Statistical model We rely on matched difference-in-differences (MDID) models to measure the association between punishment cell placement (relative to other disciplinary actions) and postrelease criminal convictions and employment. Here, we first describe the standard (i.e., unmatched) difference-in-differences (DID) approach, and we then explain why and how we supplement the standard DID approach with propensity score matching. In practice, standard difference-in-differences models are used to exploit the panel structure of the data to evaluate differences in outcome trajectories rather than just differences in postrelease outcome levels.7,8 There are three main strengths of this approach.9 First, by focusing on preadmission outcomes in addition to postrelease ones, use of the DID approach explicitly takes into account that there are dif- ferences between those who experience punishment cell confinement and those who are recorded as “only” experiencing other disciplinary actions—differences that would persist even absent punishment

7 Fitted to individual level (i) panel data, the additive DID model in our context is y𝑖𝑡 = 𝛼𝑖𝑡 + 𝛽1𝑝𝑢𝑛𝑖𝑠ℎ𝑚𝑒𝑛𝑡𝑐𝑒𝑙𝑙𝑖𝑡 + 𝛽2𝑝𝑜𝑠𝑡𝑖𝑡 + 𝛽3𝑝𝑢𝑛𝑖𝑠ℎ𝑚𝑒𝑛𝑡𝑐𝑒𝑙𝑙 × 𝑝𝑜𝑠𝑡𝑖𝑡 + 𝛽4𝑋𝑖 + 𝜀𝑖𝑡 where t = 0 before incarceration and t = 1 after release from prison. y is the outcome. Post is a dummy variable equal to 0 before and 1 after incarceration, and punishmentcell is a dummy variable equal to 1 for those who were recorded with punishment cell placement and 0 for those who were recorded with other sanctions. 8X is a set of controls, and de-meaning all continuous variables in X allow for us to interpret the intercept (𝛼) as the pre- incarceration outcome level for the “other sanctions” group. 𝛽1measures the difference between the groups before incarceration. 𝛽2 then measures the change in outcome of the “other sanctions” group from before to after incarceration, and 𝛽3, the parameter of specific interest in our setup, measures any additional change in the outcome for the punishment cell confined group. 𝜀 is the error term. 9We estimate all models using Ordinary Least Squares (OLS) and cluster standard errors at the highest meaningful level of interaction between inmates: the facility level. Because our outcome variables are binary, we also check whether our main results are sensitive to our choice of estimator. These results are available in the online supporting information. 436 WILDEMAN AND ANDERSEN

TABLE 3 Descriptive statistics (Means and Standard Deviations) of control variables, by disciplinary actions. Danish correctional facilities, 2006–2013 (N = 36,360) Other Disciplinary No Recorded Punishment Cell Actions Disciplinary Actions Variable MSDMSDMSD First prison spell in data .776a .417 .809a .393 .852a .355 –2nd prison spell .161a .368 .143a .350 .113a .317 –3rd+ prison spell .062a .242 .048a .213 .034a .182 Detained pretrial .638a .481 .542a .498 .370a .483 Sentence length (months) 15.727a 17.207 9.565a 12.902 4.686a 8.930 Length of incarceration (months) 11.350a 13.253 5.631a 8.579 2.334a 4.361 Violent crime .374a .484 .391b .488 .324ab .468 Sex crime .016a .124 .023a .151 .044a .206 Other violent crimes .031a .174 .022a .147 .018a .134 Arson .009a .094 .007b .084 .005ab .073 Robbery .154a .361 .071a .256 .024a .152 Theft .167a .373 .149a .356 .114a .318 Other property crimes .020a .141 .028a .166 .034a .182 Drugs .089a .285 .082b .274 .041ab .199 Traffic .030a .171 .091a .288 .207a .405 Other crimes .110a .313 .135a .342 .189a .391 Total disciplinary infractions 5.516a 6.535 2.406a 2.352 −− # in-prison fines 3.578a 4.527 1.577a 1.777 − − # in-prison official warnings 1.059a 1.755 .622a .943 −− Jail .331a .471 .178a .382 .201a .400 Open prison .537ab .499 .757b .429 .750a .433 Closed prison .132a .339 .065a .247 .049a .216 Born Before 1971 .155a .362 .237a .425 .394a .489 Age at Admission 28.237a 8.770 30.883a 9.802 35.107a 1.828 Female .056a .229 .045ab .207 .057b .232 Has Children .158a .365 .159 .366 .174a .380 Ethnic Minority Background .300a .458 .234a .424 .167a .373 Years of Education 8.820a 3.236 9.307a 3.237 9.742a 3.356 Missing in Education Register .090a .286 .074a .262 .066a .249 Ever Mental Health Care Contact .237ab .425 .204a .403 .203b .402 Previously Incarcerated .559ab .497 .533a .499 .523b .499 No Siblings .148a .355 .170a .375 .206a .405 One Sibling .318 .466 .310 .462 .310 .462 Two Siblings .250a .433 .267a .442 .261 .439 Three or More Siblings .285a .451 .254a .435 .223a .416 Parents Married at Age 15 .290a .454 .266a .442 .216a .411 Father Ever Convicted .448a .497 .402a .490 .322a .467 Father Ever Incarcerated .256a .436 .233a .423 .196a .397 (Continues) WILDEMAN AND ANDERSEN 437

TABLE 3 (Continued) Other Disciplinary No Recorded Punishment Cell Actions Disciplinary Actions Variable M SD M SD M SD Father Missing in Register .087a .282 .096b .295 .130ab .337 Mother’s Age at Birth 21.303a 1.145 20.413a 1.673 18.528a 11.686 Mother Missing in Register .050a .217 .066a .248 .097a .297 Missing Mother’s Age at Birth .151a .358 .183a .386 .255a .436 Convicted, 2–3 Years Before .731a .444 .640a .480 .519a .500 Convicted, 3 Years After .627a .484 .461a .498 .318a .466 Ever Employed, 2–3 Years Before .618a .486 .675a .468 .691a .462 Ever Employed, 2–3 Years After .405a .491 .515a .500 .556a .497 Cumulative Earnings, 2–3 Years Before 8.827a 16.670 14.074a 22.699 19.080a 27.161 Cumulative Earnings, 2–3 Years After 8.106a 18.138 13.155a 24.182 17.396a 28.081 Dep. on Social Ass. 2–3 Years Before .616a .434 .636a .434 .649a .439 Dep. on Social Ass. 3 Years After .773a .369 .731a .396 .706a .413 Violence, 2–3 Years Before .313a .464 .260a .439 .203a .402 Violence, 3 Years After .249a .432 .168a .374 .112a .316 Drug Offense, 2–3 Years Before .340a .474 .245a .430 .165a .372 Drug Offense, 3 Years After .396a .489 .281a .449 .161a .368 DUI Offense, 2–3 Years Before .068a .251 .096a .295 .142a .350 DUI Offense, 3 Years After .091a .288 .101 .301 .103a .304 Incarceration, 2–3 Years Before .512a .500 .397a .489 .292a .455 Incarceration, 3 Years After .513a .500 .362a .481 .257a .437 Arrested, 2–3 Years Before .783a .412 .690a .463 .599a .490 Arrested, 3 Years After .700a .458 .555a .497 .413a .492 Mental Health Care, 2–3 Years Before .127a .333 .114a .318 .105a .306 Mental Health Care, 3 Years After .143a .350 .118a .323 .104a .305 Number of Observations 4,120 12,483 19,757 Notes: Dummy variables for admission year and release are removed from this table in the interest of conserving space but available in table A2 in the online supporting information. Means that, within table rows, share superscript differ statistically at least at the 5 percent significance level (Student’s t tests, two-tailed tests). Cumulative Earnings are measured in 1,000s of 2010 PPP-adjusted US$. Missing mothers are recorded with 0 on Mother’s Age at Birth, and we measure the association between this group and the outcome using the dummy indicator Missing Mother’s Age at Birth. The low mean for Mother’s Age at Birth reflects this construction. Abbreviations: DUI = driving under the influence; M = mean; PPP = purchasing power parity; SD = standard deviation. Source: Own calculations based on data from Statistics Denmark. *p < .05; **p < .01; **p < .001 (two-tailed tests). cell. If we did not take such preexisting differences into account, it would be impossible to evaluate how much of the difference in postrelease outcomes was driven by conditions of confinement and how much was driven by preexisting differences between the groups. Second, and related to the first strength, use of the DID approach exploits the panel structure of the data to net out the impact of any stable individ- ual characteristics that are not observed in the data. If we focused only on postrelease outcomes and even if we controlled extensively for observed background characteristics, any remaining difference in outcomes could still be driven by unobserved characteristics, which could lead to severely biased estimates. Third, use of the DID approach explicitly takes time trends in the outcomes into account. 438 WILDEMAN AND ANDERSEN

In our setup, this means that we take into consideration that there are general and well-documented effects of imprisonment on the outcomes we study (e.g., Western, 2006) even in the absence of punish- ment cell placement. If we focused only on the change in outcomes for the treatment group, it would be impossible to evaluate how much of the change was driven by experiencing the punishment cell placement. There are two key identifying assumptions of the DID estimator. The first is the assumption of com- mon trends. According to this assumption, in our setup, the outcome trajectory of the group experienc- ing other disciplinary actions adequately represents what the outcome trajectory of the punishment cell group would have been in the absence of punishment cell. This assumption is fundamentally untestable, yet from the outcome plots (figure 1) there is no reason to suspect differing outcome trajectories before the incarceration. The second assumption is the conditional independence assumption. According to this assumption, in our setup, the decision to place an inmate in a punishment cell or to provide another sanction should be as good as random once we condition on all relevant characteristics. As shown in table 2, we observe extensive information about the inmates in our data, and we can effectively condi- tion on this information in the DID models. But the conditional independence assumption concerns all relevant differences between the groups, including ones that are unobserved in the data and for which we therefore cannot control. Considering the observed differences between our comparison groups and the fact that some inmates were sanctioned more severely than others, it seems unlikely that the con- ditional independence assumption holds in our setup—although we focus on individual trajectories in outcomes and can control for many confounders. This is a core limitation to our analysis, and one that we return to in the Discussion and Conclusion section. Our admittedly imperfect solution to handling the conditional independence assumption is to merge the benefits of the standard DID model with the benefits of propensity score matching (PSM). PSM is a two-step procedure. First, we use all observed characteristics to estimate each inmate’s risk of expe- riencing punishment cell placement (relative to experiencing other formal disciplinary actions). These risks are known as propensity scores. Second, the idea behind PSM is then that inmates with similar propensity scores are likely to be more similar also on all relevant unobserved characteristics than are inmates with different propensity scores. Thus, in PSM we assume that the conditional independence assumption is more likely to hold if we focus on inmates that have the same risk of punishment cell placement—a plausible assumption considering the list of characteristics we use to estimate the propen- sity scores. The matching itself—the algorithm used, see our choices in the following discussion—then assigns individual weights to inmates in the outcome model according to their propensity score. Our merging of DID and PSM then focuses only on inmates with similar propensity scores (known as obser- vations that fall within the area of common support) and applies the weights from the PSM to the DID models. No statistical model is without caveats. The caveats of MDID models are that 1) they require panel data, 2) they cannot address unobserved time-varying traits, 3) they still rely on the conditional indepen- dence assumption, and 4) the matching procedure includes more or less arbitrary choices concerning how many observations to compare each treated observation with as well as how to define the individ- ual weights. In our setup, we overcome caveat 1) by relying on highly detailed Danish administrative data that have a panel structure. Caveats 2) and 3) are more challenging as they concern unobserved heterogeneity. It is our hope, however, that the detailed nature of our data as well as our choice of com- parison groups (both in terms of not including the general prison population and in terms of analyzing the associations by facility types) and our use of propensity score matching minimizes the risk of these caveats causing any serious bias in our estimates. Caveat 4) we address by presenting results from a range of different model choices to observe whether our conclusions are sensitive to such choices (which they are not). WILDEMAN AND ANDERSEN 439

Turning to standard errors, we find that the MDID models in total rely on three analytical steps, each of which comes with statistical uncertainty. Propensity scores are estimated from data, the selection of comparison observations when there are several observations in the control group with identical propensity scores is arbitrary, and the final DID model is estimated from the matched data. Therefore, the analytical standard errors derived from fitting the MDID model to the data are likely to be incorrect. Our solution to this challenge is to bootstrap the entire MDID procedure. In bootstrapping, we draw 250 random samples (with replacement, each observation may thus appear in each random sample more than once; each of these samples is known as a bootstrap sample) from our data set and replicate the analyses for each bootstrap sample. The standard deviation in each parameter estimate across the 250 bootstrap samples is then a better measure of the parameter’s standard error than the original analytical one. Also, because inmates are unlikely to be statistically independent if they serve their sentence in the same facility, we cluster the standard errors (throughout the entire bootstrapping process) at the facility level (again, for simplicity we focus on where the inmate was first placed).

3.3.2 Main analysis First, we estimate the propensity score model that we use to predict each inmate’s risk of punishment cell placement, and we compare the distribution of these risks in the comparison groups before and after the data are weighted by one of the matching algorithms (Epanechnikov kernel matching, which we chose because it relies on more information from the control group than the other algorithms). The point here is to show how unequally distributed the risk of punishment cell placement would be if we did not merge the benefits of PSM onto the DID model—implying that results from standard DID models would likely be biased in our setup. To bolster this point, we present a comparison of the means and standard deviations of each control variable in both the unmatched and the matched samples (again, we show results only for Epanechnikov kernel matching, but results for other algorithms are similar). Having demonstrated the appropriateness of the PSM in our setup, we then move to the MDID model, which now simply means the DID model on the data that are weighted from the matching procedures. For each outcome, we run many MDID models as defined from the matching algorithm. Specifically, we run one-to-one nearest neighbor (1:1 NN) matching both with and without replace- ment, 1:2, 1:3, 1:4, 1:5, and 1:10 NN matching, local linear matching, radius matching, and Epanech- nikov kernel matching. We use a caliper of .005 for all algorithms, except for kernel matching in which we use the default caliper of .06. The algorithms differ in how many observations they rely on for estimating the association between punishment cell placement and the outcomes, which naturally is consequential for the confidence intervals. We plot the point estimates and confidence intervals by the number of observations that are used in the respective models as a way of showing that although the width of the confidence intervals changes across the MDID models, the point estimates of the associations are stable.

3.3.3 Supplementary analyses We run three sets of supplementary analyses, as presented in the online supporting information, to provide a detailed picture of how the effects of restrictive housing are structured. First, we estimate results by pretrial detention status. Here, we split the data into those who experienced pretrial detention while awaiting trial and those who did not. We do so because all individuals who experience pretrial detention in Denmark do so, for practical reasons, in restrictive housing in a jail, as mentioned. As such, all inmates who experienced pretrial detention had de facto experienced restrictive housing preadmis- sion, and we therefore expect the association between punishment cell placement postconviction and 440 WILDEMAN AND ANDERSEN the outcomes to be smaller than the main results. Second, we present results for alternative outcomes. These alternative outcomes represent other recidivism measures (arrest, incarceration, recidivism by crime type) and other measures of labor market outcomes (earnings and dependency on social wel- fare). Also, because we expect the effects of punishment cell placement to run through strained mental health, we estimate the association between punishment cell placement and the risk of experiencing contact with the mental health care system outside the prison system. Danish prisons have their own hospitals and their own system for prescribing drugs to inmates. We do not have information on the use of these in-prison systems in our data.10 Instead, our data only indicate whether people have con- tact/consultancy with the general mental health care system before and after release, and our results for mental health care use should be viewed as extreme lower bounds. Third, we present results where we restrict the data to include only inmates who are serving their first prison sentence. We do this to observe whether the cumulative consequences of repeat incarceration could be driving some of our main results (which would be the case if, for example, returning inmates have a higher risk of being placed in punishment cell and have poorer outcomes, not because of punishment cell placement but because of being returning inmates; our main model controls for this risk, yet analyzing first spells only serves to bolster this point).

4 RESULTS

4.1 Propensity scores and the benefits of matching Figure 2 shows the distributions of the estimated individual risk of punishment cell placement (relative to officially experiencing other disciplinary actions), known as the “propensity scores,” by treatment status (punishment cell vs. other recorded sanctions) and by facility type. All parameter estimates from the propensity score models are presented in table A1 in the online supporting information, which also shows that these models in general have high predictive power, with R2 values generally in the .12 to .15 range. Plots presented in the left figure column show results before matching. Here, it is obvious that the propensity score distributions differ across treatment status as a much larger proportion of those who do not experience punishment cell placement have comparatively lower risks of doing so, even across facility types. Plots presented in the right figure column show results after matching. The benefits of using matching to account for heterogeneity are obvious from these plots as they clearly show how weighting the data via the matching algorithm (in this case, Epanechnikov kernel matching) secures a much more similar distribution of propensity scores. Similarity in the propensity score distributions after matching is no guarantee that all important covariates are balanced across the comparison groups, however. Figure 3 therefore shows, by facility type, the results from t test statistics that compare the mean and standard deviation for each covariate by treatment status and before and after matching. As is clear from the figure, there were substantial imbalances in the covariate distribution before matching (many test values exceeding ±1.96 corre- sponding to statistical significance below .05), yet the matching effectively balances the groups on almost all covariates. Table A2 in the online supporting information shows that between 26 percent (closed prisons) and 68 percent (all facilities) of the covariate means differed at the five percent level

10Previous researchers had access to in-prison mental health care use during pretrial detention and found an increase in the risk of using it once subjected to restrictive housing (Sestoft, Andersen, Lillebæk, & Gabrielsen, 1998). For prisoners who spend 4 weeks in restrictive housing, for example, the risk was ∼20 times as high as for prisoners who did not experience it. Although some of that difference may well be attributable to something other than the treatment, in a population as homogenous as the penal population, a relative risk of 20 for severe mental health problems suggests some effect. WILDEMAN AND ANDERSEN 441

BEFORE MATCHING AFTER MATCHING All facilities N=16,603 N=16,550

Other disciplinary actions 4.000 Punishment cell

Percent 2.000

0.000 0 25 50 75 100 0255075100 Closed prisons N=1,532 N=1,502 4.000

3.000

2.000 Percent 1.000

0.000 0 25 50 75 100 0255075100 Open prisons N=11,319 N=11,293

6.000

4.000 Percent 2.000

0.000 0 25 50 75 100 0255075100 Jails N=3,752 N=3,671 4.000

3.000

2.000 Percent 1.000

0.000 0 25 50 75 100 0255075100 Propensity score Propensity score

FIGURE 2 Distribution of propensity scores by disciplinary sanction type and by facility type. Before and after weighting from Epanechnikov kernel matching. Denmark, 2006–2013 Notes: Table A1 in the online supporting information shows parameter estimates from the propensity score predictions. Propensity score distributions obtained from other matching algorithms are available on request from the corresponding author. We drop observations that fall outside the area of common support, hence, the difference in the number of observations before and after matching. Source: Own calculations based on data from Statistics Denmark. 442 WILDEMAN AND ANDERSEN

All facilities (N = 16,550) Closed prisons (N = 1,502)

Open prisons (N = 11,293) Jails (N = 3,671)

FIGURE 3 T test scores comparing the distribution of background characteristics among prisoners placed in punishment cell and prisoners recorded with other disciplinary actions. By facility type and before and after Epanechnikov kernel matching Notes: Test scores are capped to the –7 to +10 interval to ease graphical representation. Precise test scores may be requested from the corresponding author. Table A2 in the online supporting information summarizes the distribution of t test scores by other matching algorithms, whereas full tables of the t test scores are available from the corresponding author on request. Source: Own calculations based on data from Statistics Denmark. in the unmatched data (table A2 provides a summary of results for all matching algorithms). The matching reduces these percentages to below 5 and, in most instances, to 3 percent or even lower. In all, the results presented here show that the matched data achieve a higher degree of similarity between treated and untreated observations than was the case before matching (where we observed large differences). Given this similarity, it seems more likely that also traits that are unobserved in the data are better balanced across the comparison groups, effectively making results from our MDID models less likely to be biased than if we had not applied matching.

4.2 Matched difference-in-differences results for convictions Figure 4 presents results from the MDID models considering the long-term consequences of having been placed in a punishment cell on the change in the risk of being convicted of a crime. We show our estimate of the association for each matching algorithm. Although the different algorithms pro- duce different sample sizes (x-axis), the point estimates remain stable across algorithms and facility types. The most notable conclusion from figure 4 is thus that across almost all matching algorithms WILDEMAN AND ANDERSEN 443

All facilities Closed prisons

.200 .200

.100 .100 ● ● ● ● ● ● ● ● ● ●● ● ● ● ● ● ● ● ●

.000 .000 LLR Kernel Radius Radius LLR 1:4 NN 1:5 NN 1:3 NN 1:2 NN 1:3 NN 1:4 NN 1:5 NN 1:2 NN 1:10 NN 1:10 NN Kernel

Point estimate and 95% CI −.100 −.100 1:1 replacement 1:1 replacement 1:1 no replacement 1:1 no replacement

−.200 −.200

6000 9000 12000 15000 1000 1200 1400 Open prisons Jails

.200 .200

.100 .100

● ● ● ● ● ● ● ● ● ● ●● ●● ● ● ● ● ● ●

.000 .000 LLR LLR Kernel Kernel Radius Radius 1:2 NN 1:4 NN 1:3 NN 1:4 NN 1:5 NN 1:3 NN 1:2 NN 1:5 NN 1:10 NN 1:10 NN −.100 −.100 Point estimate and 95% CI 1:1 replacement 1:1 replacement 1:1 no replacement 1:1 no replacement

−.200 −.200 5000 7500 10000 2000 2500 3000 3500 Number of observations (unweighted) Number of observations (unweighted)

FIGURE 4 Main results for criminal conviction, by facility type. Point estimates and 95% confidence intervals from difference-in-differences models, by matching algorithm and number of observations. Denmark, 2006–2013 Notes: Bootstrapped (250 replications) standard errors are clustered at the facility level. As a robustness check (results available from the corresponding author on request), we also estimated the models using other calipers in the matching procedures. Source: Own calculations based on data from Statistics Denmark. and facility types, the results from our MDID models reveal a significant association between pun- ishment cell placement and conviction. Point estimates are sizable, which indicates that punishment cell placement is associated with a 5.0 to 7.5 percentage point higher postrelease conviction risk than would be the case if these inmates had experienced other disciplinary actions. Considering how the matching results show that around half of released inmates who experienced other disciplinary actions during imprisonment get convicted of a new crime within the first 3 years after release (table A3 in the online supporting information), these estimates indicate substantial consequences of experiencing punishment cell placement, assuming a causal effect.

4.3 Matched difference-in-differences results for employment Figure 5 presents estimates from MDID models for employment in a parallel fashion to those shown for criminal conviction. Consistent with results for conviction, there is a substantial association between punishment cell placement and employment across all matching algorithms, leading us to the conclu- sion that punishment cell placement is associated with 2.0 to 4.5 percentage points lower employment. Again, this effect is substantial, as the employment rate after release for inmates who were recorded as 444 WILDEMAN AND ANDERSEN

All facilities Closed prisons

.200 .200

.100 .100 1:3 NN Kernel 1:1 no replacement 1:2 NN 1:4 NN 1:5 NN 1:10 NN Radius LLR 1:1 replacement 1:1 replacement LLR 1:2 NN 1:10 NN Kernel 1:1 no replacement 1:3 NN 1:4 NN 1:5 NN Radius .000 .000

● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ●

Point estimate and 95% CI −.100 −.100

−.200 −.200

6000 9000 12000 15000 1000 1200 1400 Open prisons Jails

.200 .200

.100 .100 LLR 1:1 no replacement 1:1 replacement 1:1 replacement LLR 1:1 no replacement 1:2 NN Kernel 1:3 NN 1:4 NN 1:3 NN 1:4 NN 1:5 NN 1:10 NN Radius Kernel 1:5 NN 1:10 NN 1:2 NN Radius .000 .000 ● ●● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ●●

−.100 −.100 Point estimate and 95% CI

−.200 −.200 5000 7500 10000 2000 2500 3000 3500 Number of observations (unweighted) Number of observations (unweighted)

FIGURE 5 Main results for employment, by facility type. Point estimates and 95% confidence intervals from difference-in-differences models, by matching algorithm and number of observations. Denmark, 2006–2013 Notes: Bootstrapped (250 replications) standard errors are clustered at the facility level. As a robustness check (results available from the corresponding author on request), we also estimated the models using other calipers in the matching procedures. Source: Own calculations based on data from Statistics Denmark. having experienced other disciplinary sanctions (but not punishment cell) is approximately 50 percent (table A3). Focusing on significance, most estimates for all facilities and open prisons are significant at least at the 5 percent level. But for closed prisons and jails, which generally host fewer inmates and therefore have larger standard errors, the results are statistically insignificant (especially closed prisons). Yet whereas this insignificance could signal that there is no substantial association between punishment cell placement and employment once compositional differences are taken into account, because the point estimates for these facility types overall are of the same magnitude as those for all facilities and open prisons, it might be the case that there is some real effect on employment but the small size of N has merely inflated the standard errors. Regardless of which interpretation one chooses, the fact remains that the signs of a causal effect (or even of persistent association) are stronger for recidivism than for employment.

4.4 Results from supplementary analyses 4.4.1 Pretrial detention Figures 6 and 7 present results from robustness checks also considering pretrial detention (see the supplementary appendix in the online supporting information for more details). The results provide WILDEMAN AND ANDERSEN 445

NOT DETAINED PRETRIAL DETAINED PRETRIAL All facilities .200 .200

.100 .100 ●● ● ● ● ● ● ● ●● ● ● ● ● ●● ● ● .000 .000

−.100 −.100 LLR 1:2 NN 1:3 NN 1:5 NN 1:10 NN LLR 1:3 NN 1:4 NN Radius 1:1 no replacement 1:1 replacement 1:2 NN 1:10 NN Kernel 1:1 replacement 1:4 NN Radius Kernel 1:1 no replacement 1:5 NN Point estimate and 95% CI −.200 −.200 2000 3000 4000 5000 6000 4000 6000 8000 10000 Closed prisons

.200 ● .200 ● ●●● ● ● ●

.100 .100 ● ● ● ● ● ● ● ● ● ● ● .000 .000

−.100 −.100 Point estimate and 95% CI 1:2 NN 1:3 NN 1:4 NN Radius Kernel 1:1 no replacement LLR 1:10 NN Radius 1:1 no replacement 1:1 replacement LLR 1:5 NN 1:10 NN 1:1 replacement 1:2 NN 1:3 NN 1:5 NN Kernel −.200 −.200 1:4 NN 200 250 300 350 400 600 700 800 900 1000 Open prisons .200 .200

.100 .100 ●● ●● ● ● ● ● ● ● ● ● ● ● ● ● ● ●● .000 .000

−.100 −.100 Point estimate and 95% CI 1:1 no replacement LLR 1:1 replacement 1:2 NN 1:3 NN 1:4 NN 1:5 NN Radius 1:2 NN 1:3 NN 1:5 NN Kernel Kernel 1:1 no replacement LLR 1:1 replacement 1:10 NN Radius 1:10 NN −.200 1:4 NN −.200 1000 2000 3000 4000 5000 2000 3000 4000 5000 6000 Jails .200 .200

.100 .100 ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ●● .000 .000

−.100 −.100 1:1 no replacement LLR 1:2 NN 1:3 NN 1:4 NN 1:10 NN Radius Kernel LLR 1:1 no replacement 1:2 NN 1:3 NN 1:4 NN 1:5 NN 1:10 NN Radius Kernel 1:5 NN 1:1 replacement 1:1 replacement Point estimate and 95% CI −.200 −.200 800 1000 1200 1500 1800 2100 2400 Number of observations (unweighted) Number of observations (unweighted)

FIGURE 6 Results for criminal conviction by pretrial detention status and by facility type. Point estimates and 95% confidence intervals from difference-in-differences models, by matching algorithm and number of observations. Denmark, 2006–2013 Note: Bootstrapped (250 replications) standard errors are clustered at the facility level. Source: Own calculations based on data from Statistics Denmark. 446 WILDEMAN AND ANDERSEN

NOT DETAINED PRETRIAL DETAINED PRETRIAL All facilities .200 .200 LLR LLR Kernel Kernel Radius Radius 1:2 NN 1:3 NN 1:4 NN 1:2 NN 1:3 NN 1:4 NN 1:5 NN .100 1:5 NN .100 1:10 NN 1:10 NN

.000 .000 1:1 replacement 1:1 replacement ● ●● ● ● ● ● ● ● ● 1:1 no replacement 1:1 no replacement ●● ● ● ● ● ●● −.100 −.100

Point estimate and 95% CI −.200 −.200 2000 3000 4000 5000 6000 4000 6000 8000 10000 Closed prisons .200 .200 LLR LLR Kernel Kernel Radius Radius 1:4 NN 1:3 NN 1:5 NN 1:2 NN 1:3 NN 1:5 NN 1:2 NN 1:4 NN 1:10 NN .100 .100 1:10 NN 1:1 replacement 1:1 replacement ● .000 .000 ● ● ● ● ● ● 1:1 no replacement 1:1 no replacement ● ● ● ●●● ● ● ● ● ● −.100 ● −.100 Point estimate and 95% CI −.200 −.200 200 250 300 350 400 600 700 800 900 1000 Open prisons .200 .200 LLR LLR Kernel Kernel Radius Radius 1:5 NN 1:2 NN 1:5 NN 1:2 NN 1:4 NN 1:3 NN 1:4 NN 1:3 NN 1:10 NN .100 1:10 NN .100 1:1 replacement .000 .000 1:1 replacement ● 1:1 no replacement ● ● 1:1 no replacement ● ● ● ● ● ● ● ● ●● ● ● ●● ●●● −.100 −.100 Point estimate and 95% CI −.200 −.200 1000 2000 3000 4000 5000 2000 3000 4000 5000 6000 Jails .200 .200 LLR LLR Kernel Kernel Radius Radius 1:5 NN 1:2 NN 1:3 NN 1:3 NN 1:4 NN 1:5 NN 1:4 NN .100 1:2 NN .100 1:10 NN 1:10 NN

●● ● ● ● .000 .000 ● ● ● ●● 1:1 replacement 1:1 replacement ●● ● ● ● ● ● ● ● 1:1 no replacement ● 1:1 no replacement −.100 −.100

Point estimate and 95% CI −.200 −.200 800 1000 1200 1500 1800 2100 2400 Number of observations (unweighted) Number of observations (unweighted)

FIGURE 7 Results for employment by pretrial detention status and by facility type. Point estimates and 95% confidence intervals from difference-in-differences models, by matching algorithm and number of observations. Denmark, 2006–2013 Note: Bootstrapped (250 replications) standard errors are clustered at the facility level. Source: Own calculations based on data from Statistics Denmark. WILDEMAN AND ANDERSEN 447 support for several conclusions. First, the matched samples for those detained pretrial tend to be larger than for those not detained pretrial, indicating that pretrial detention is a strong correlate of postcon- viction incarceration. This result, however, is more accurate for inmates who were first assigned to closed prisons and locals jails. Second, the results for conviction are generally consistent with the main results, although with larger standard errors. Third, the employment results differ somewhat from the main results. The association between punishment cell placement and postrelease employment tends to be smaller for those detained pretrial (and, indeed, results for those detained pretrial are statistically insignificant even in the pooled data). This result is driven by a complete lack of an effect of punish- ment cell placement on employment for those detained in local jails and who experience punishment cell placement. Here, we observe the negative effects of punishment cell placement on employment for those not detained pretrial, yet zero and even positive estimates (not significant, however) for those detained pretrial. Considering how pretrial detention in Denmark shares many features with restrictive housing, the results presented here are intuitive.

4.4.2 Alternative outcomes Figure A2 in the online supporting information shows results for our alternative outcome measures. Inmates placed in a punishment cell are more likely to experience reincarceration, more likely to expe- rience arrest, and more likely to be convicted of a violent crime as well as of the possession of drugs. For DUI offenses, we observe very small and statistically insignificant point estimates. The same is true for contact with the mental health care system, yet because of the data limitations in this particular measure, it is too early to conclude that these insignificant results indicate that poor mental health is not a driver of effects on recidivism and employment. For alternative measures of labor market attach- ment, we observe a negative association between punishment cell placement and cumulative earnings across all matching algorithms. For dependency on social welfare, high base levels (>70 percent) of dependence on social assistance before incarceration signal that prisoners are not well integrated into the labor market in Denmark. And just as the base levels differ little among those who experienced the treatment and those who did not, the results for the impact of punishment cell placement also fail to document any substantial nor statistically significant association with this outcome after release.

4.4.3 First incarceration spells only The results for inmates who are serving their first prison sentence are similar to our main results, although the confidence intervals are larger.

5 DISCUSSION AND CONCLUSION

Research on restrictive housing has historically tended to be focused on the ethics of placement in restrictive housing, especially long-term placement in administrative segregation, and the effects of placement in restrictive housing, again especially long-term placement in administrative segregation, on mental health. Smaller bodies of research have been aimed at considering the effects of restrictive housing on safety and security in a facility and on prisoner reentry outcomes. In this article, we contributed to research in this area by assessing the long-term consequences of being placed in a specific type of restrictive housing, disciplinary segregation in a punishment cell, for a short period of time on two core indicators of successful reentry that are also of the utmost importance for families and communities: being convicted of a new crime and being employed. To do so, we used 448 WILDEMAN AND ANDERSEN a data set that includes not only the full suite of information available on the Danish population in their registry data but also detailed data on the recorded in-prison experiences, including both disciplinary segregation and other sanctions that result from in-prison infractions, of all Danish inmates. Although we lack an exogenous shock in the risk of being placed in punishment cell, a major issue that we return to in short order, the matched difference-in-difference analyses we present here represent a strong, if imperfect, test of disciplinary segregation’s effects, especially relative to previous work in this area, which has been reliant on matching (e.g., Mears & Bales, 2009) or covariate adjustment (e.g., Butlter et al., 2019). The results from analyses of these data provide support for two straightforward conclusions. First, the results provide strong, consistent evidence that Danish prison and jail inmates placed in disciplinary segregation in a punishment cell experience a larger percent increase in the risk of recidivism, measured here as a new conviction, than does a matched group of inmates who were recorded as having experienced other disciplinary sanctions for an infraction instead of being placed in a punishment cell. As figure 4 and the supplementary results in the online supporting information indicate, moreover, these results are robust to a whole host of model specifications and reveal that Danes placed in punishment cell experience a 5 to 7.5 percentage points greater increase in the risk of conviction compared with a matched comparison group that was officially punished for a disciplinary infraction but not placed in a punishment cell. Second, the results also provide support for the general idea that punishment cell confinement decreases labor force participation after release, although with more caveats than is the case for the findings on conviction. As figure 5 indicates, for the pooled model including all facilities and the mod- els considering only open prisons, there is consistent evidence of a statistically significant but modest (<5 percent) decline in labor force participation among those sent to a punishment cell. Although the point estimates are similar for Danes in closed prisons and jails, the larger confidence intervals that result from a smaller number of observations lead to less certainty in interpretation. Thus, although the evidence for new convictions is strong, the evidence for an effect on labor force participation rates is somewhat more muted in these models. These results are important for three reasons. First, they contribute to research on the costs of restric- tive housing by using high-quality data and rigorous methods that control for a range of unobserved heterogeneity to show that punishment cell placement has long-term consequences for the chance of being employed or convicted. There are well-known ethical reasons to oppose the use of restrictive housing. Our results show that the practice may also be counterproductive as placing prisoners in restrictive housing (in this case in punishment cell) can significantly compromise their chance of suc- cessfully reintegrating into society in two vitally important dimensions after release. Second, these results call us to rethink effect heterogeneity in the consequences of incarcera- tion for core life-course outcomes. Research findings show the negative effects of incarceration on labor market prospects (e.g., Pager, 2003; Western, 2002, 2006; but see Loeffler, 2013), health (e.g., Massoglia, 2008; Massoglia & Pridemore, 2015; Schnittker & John, 2007), and family life (e.g., Com- fort, 2008; Lopoo & Western, 2005). Because incarceration is so heavily concentrated among already- marginalized populations, these individual-level effects, moreover, have implications for inequality (e.g., Wakefield & Uggen, 2010; Western, 2006). Yet important as these average effects are, in a grow- ing body of research, scholars have considered effect heterogeneity in the consequences of incarcera- tion (e.g., Turney, 2017), and some have speculated that the conditions of confinement represent a key driver of any heterogeneity that exists (Wildeman & Muller, 2012; Wildeman & Wang, 2017). Unfor- tunately, testing how conditions of confinement affect the outcomes of the formerly incarcerated has hitherto been difficult, making it unclear whether these conditions induce heterogeneity in incarcera- tion’s effects. By showing that being placed in a punishment cell, one key condition of confinement WILDEMAN AND ANDERSEN 449 experienced by a large share of inmates in any given year, moderates the effects of incarceration on individual’s employment and risk of reconviction in the next three 3 years, we provide an important starting point for conversations about how conditions of confinement may significantly moderate incar- ceration’s consequences. Third, these results also provide insight into how we think about the mechanisms driving the effects of incarceration. As many researchers have noted (e.g., Muller & Wildeman, 2012), decipher- ing whether the consequences of incarceration for life-course outcomes are driven by the stigma of incarceration or by the transformation produced by incarceration has proven a tall order because even though experimental manipulations make it possible to test for stigma (Pager, 2003), few designs using observational data make it possible to differentiate the effects of stigma from the effects of transforma- tion. In this study, by holding incarceration constant—since our entire sample had been incarcerated— and varying exposure to punishment cell, we show that for some former prisoners, the transformation induced by incarceration is quite large and negative. Of course, the current study is not without limitations. We focus here on four, three of which have to do with internal validity and one of which has to do with external validity. Of course, the most basic threat to internal validity with a DID model is that the treatment, in this case punishment cell confinement, is not distributed “at random” between the treatment and control groups. Unfortunately, we were not able to gain access to data that would make it possible for us to identify exogenous vari- ation in the risk of punishment cell confinement, which means that these estimates should be inter- preted as strongly associational and pointing toward causal relationships without perfectly identifying such. Future research might be aimed at looking for exogenous variation in the risk of confinement by exploiting cross-facility or cross-guard variation in the risk of placement. A second concern revolves around the possibility of a violation of the common trends assumption. Although we see no visible evidence of this in our data, the reality is that the DID model is always vulnerable to time-varying changes in the treatment and control groups that affect both the explanatory and dependent variables. In addition to these two core threats to internal validity is the fact that we cannot fully test the degree to which declines in mental health caused by restrictive housing exposure drive poor postrelease out- comes. Thus, although our analyses represent an important step forward in this literature, the reality is that our analyses may not represent causal effects and cannot precisely test core mechanisms. In addition to these concerns about internal validity, it is also unclear how these results generalize to other contexts—especially the U.S. context—for several reasons. First, there are dramatic differences between both of these two criminal justice systems and these two societies more broadly (e.g., Pratt, 2008; Walmsley, 2018). Yet the differences cut deeper still. As table 1 indicates, for instance, there are truly marked differences in the duration of exposure to punishment cell placement and restrictive housing placement in Danish and U.S. prisons. This suggests that even if all other things were equal, it would be difficult to be certain that the estimates presented here for short stays would map on in any discernible way to the effects we might find in the U.S. context. And, in a similar vein, there is no guarantee that the associations we find for disciplinary segregation would hold for other types of restrictive housing placement such as administrative segregation. Limitations aside, these results from our analyses indicate that as criminologists return to prisons and jails (e.g., Kreager & Kruttschnitt, 2018; Kreager et al., 2017; Walker, 2016; Wildeman, Fitzpatrick, & Goldman, 2018), they must consider the effects of restrictive housing not only on those who experience it for years on end but also on those who experience it briefly.

ORCID

Lars Højsgaard Andersen https://orcid.org/0000-0003-2357-1896 450 WILDEMAN AND ANDERSEN

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AUTHOR BIOGRAPHIES

Christopher Wildeman is a professor of policy analysis and management and sociology (by cour- tesy) at Cornell University and a professor at the ROCKWOOL Foundation Research Unit. His research and teaching interests revolve around the consequences of mass imprisonment for inequal- ity, with emphasis on families, health, and children. He is also interested in child welfare, especially as relates to child maltreatment and the foster care system.

Lars Højsgaard Andersen is a senior researcher at the ROCKWOOL Foundation Research Unit. His research interests include crime and the consequences of punishment, family processes, and issues related to social policy and immigration. WILDEMAN AND ANDERSEN 453

SUPPORTING INFORMATION

Additional supporting information may be found online in the Supporting Information section at the end of the article.

How to cite this article: Wildeman C, Andersen LH. Long-term consequences of being placed in disciplinary segregation. Criminology. 2020;58:423–453. https://doi.org/10.1111/1745- 9125.12241